Coccolithophorids precipitate carbonate in clumped isotope equilibrium with seawater

Clark, Alexander J.; Torres-Romero, Ismael; Jaggi, Madalina; Bernasconi, Stefano M.; Stoll, Heather M.

doi:https://doi.org/10.5194/egusphere-2023-2581

Preprints

https://doi.org/10.5194/egusphere-2023-2581

Preprints

09 Nov 2023

| 09 Nov 2023

Coccolithophorids precipitate carbonate in clumped isotope equilibrium with seawater

Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

Abstract. Numerous recent studies have tested the clumped isotope (Δ₄₇) thermometer on a variety of biogenic carbonates such as foraminifera and bivalves and showed that all follow a common calibration. While the sample size requirements for a reliable Δ₄₇ measurement have decreased over the years, the availability and preservation of many biogenic carbonates is still limited and/or require substantial time to be extracted from sediments in sufficient amounts. We thus determined the Δ₄₇-temperature relationship for coccolith carbonate, which is abundant and often well-preserved in sediments. The carbon and oxygen isotopic compositions of coccolith calcite have limited use in palaeoenvironmental reconstructions due to physiological effects that cause variability in the carbon and oxygen isotopic values. However, the relatively limited data available suggest that clumped isotopes may not be influenced by these effects. We cultured three species of coccolithophores in well-constrained carbonate system conditions with a CO_2(aq) between 5 and 45 μM and temperatures between 6 °C and 27 °C.

Our results agree with a previous culture study that there are no species- or genus-specific effects on the Δ₄₇-temperature relationship in coccolithophores and find that varying environmental parameters other than temperature also do not have a significant effect. Our coccolith-specific Δ₄₇-temperature calibration agrees within ±1 °C of other biogenic carbonate calibrations yet all biogenic carbonate calibrations show a consistent offset of ≥2 °C relative to the inorganic carbonate calibrations. Thus, all biogenic specific calibrations can be used interchangeably and must be used for the reconstruction of calcification temperatures in biogenic carbonates.

Received: 02 Nov 2023 – Discussion started: 09 Nov 2023

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Journal article(s) based on this preprint

20 Sep 2024

A clumped isotope calibration of coccoliths at well-constrained culture temperatures for marine temperature reconstructions

Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

Clim. Past, 20, 2081–2101, https://doi.org/10.5194/cp-20-2081-2024,https://doi.org/10.5194/cp-20-2081-2024, 2024

Short summary

Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2023-2581', Anonymous Referee #1, 16 Jan 2024

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

------------------

- [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).

Citation: https://doi.org/10.5194/egusphere-2023-2581-RC1
- AC1: 'Reply on RC1', Alexander Clark, 30 Apr 2024
  
  Dear Reviewer,
  We sincerely thank you for the constructive comments. In the new version, we have made a few major modifications, including:
  (1) We have rewritten the introduction and several sections to provide a general description and clarification of vital effects and their implications for our study. We include previous culturing, core-top, and modelling studies of the identification of stable isotope vital effects in coccoliths. Since the focus of this study is on the clumped isotope signature, not the vital effects, we elect to present previously described mechanisms and compare with previously published models for ¹³C, but not execute new model simulations to evaluate in detail the processes behind observations from individual new cultures. We have revised the discussion to more clearly compare the vital effects in coccoliths with the Δ₄₇ signal, and describe the interpretation of this comparison.
  (2) We have revised our conclusions that coccolith carbonate is precipitated in equilibrium. Both reviewers rightfully pointed out that it does indeed seem that coccoliths do not precipitate carbonate in equilibrium and disequilibrium effects are present. Instead we have reinterpreted our findings and suggest the use of our calibration for coccolith-specific carbonates. We also urge caution and discuss the interpretation of calcification temperatures for non-in situ biogenic carbonates, which can give highly variable interpretations of the same measured dataset.
  Our point-to-point responses are listed in blue as supplement.
  
  Citation: https://doi.org/10.5194/egusphere-2023-2581-AC1
RC2:
'Comment on egusphere-2023-2581', Anonymous Referee #2, 19 Mar 2024

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

Citation: https://doi.org/10.5194/egusphere-2023-2581-RC2
- AC2: 'Reply on RC2', Alexander Clark, 30 Apr 2024
  
  Dear Reviewes,
  We sincerely thank you for the constructive comments. In this new version, we have made a few major modifications, including:
  (1) We have rewritten the introduction and several sections to provide a general description and clarification of vital effects and their implications for our study. We include previous culturing, core-top, and modelling studies of the identification of stable isotope vital effects in coccoliths. Since the focus of this study is on the clumped isotope signature, not the vital effects, we elect to present previously described mechanisms and compare with previously published models for ¹³C, but not execute new model simulations to evaluate in detail the processes behind observations from individual new cultures. We have revised the discussion to more clearly compare the vital effects in coccoliths with the Δ₄₇ signal, and describe the interpretation of this comparison.
  (2) We have revised our conclusions that coccolith carbonate is precipitated in equilibrium. Both reviewers rightfully pointed out that it does indeed seem that coccoliths do not precipitate carbonate in equilibrium and disequilibrium effects are present. Instead we have reinterpreted our findings and suggest the use of our calibration for coccolith-specific carbonates. We also urge caution and discuss the interpretation of calcification temperatures for non-in situ biogenic carbonates, which can give highly variable interpretations of the same measured dataset.
  Our point-to-point responses are listed in blue as the following.
  
  Citation: https://doi.org/10.5194/egusphere-2023-2581-AC2

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2023-2581', Anonymous Referee #1, 16 Jan 2024

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

------------------

- [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).

Citation: https://doi.org/10.5194/egusphere-2023-2581-RC1
- AC1: 'Reply on RC1', Alexander Clark, 30 Apr 2024
  
  Dear Reviewer,
  We sincerely thank you for the constructive comments. In the new version, we have made a few major modifications, including:
  (1) We have rewritten the introduction and several sections to provide a general description and clarification of vital effects and their implications for our study. We include previous culturing, core-top, and modelling studies of the identification of stable isotope vital effects in coccoliths. Since the focus of this study is on the clumped isotope signature, not the vital effects, we elect to present previously described mechanisms and compare with previously published models for ¹³C, but not execute new model simulations to evaluate in detail the processes behind observations from individual new cultures. We have revised the discussion to more clearly compare the vital effects in coccoliths with the Δ₄₇ signal, and describe the interpretation of this comparison.
  (2) We have revised our conclusions that coccolith carbonate is precipitated in equilibrium. Both reviewers rightfully pointed out that it does indeed seem that coccoliths do not precipitate carbonate in equilibrium and disequilibrium effects are present. Instead we have reinterpreted our findings and suggest the use of our calibration for coccolith-specific carbonates. We also urge caution and discuss the interpretation of calcification temperatures for non-in situ biogenic carbonates, which can give highly variable interpretations of the same measured dataset.
  Our point-to-point responses are listed in blue as supplement.
  
  Citation: https://doi.org/10.5194/egusphere-2023-2581-AC1
RC2:
'Comment on egusphere-2023-2581', Anonymous Referee #2, 19 Mar 2024

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

Citation: https://doi.org/10.5194/egusphere-2023-2581-RC2
- AC2: 'Reply on RC2', Alexander Clark, 30 Apr 2024
  
  Dear Reviewes,
  We sincerely thank you for the constructive comments. In this new version, we have made a few major modifications, including:
  (1) We have rewritten the introduction and several sections to provide a general description and clarification of vital effects and their implications for our study. We include previous culturing, core-top, and modelling studies of the identification of stable isotope vital effects in coccoliths. Since the focus of this study is on the clumped isotope signature, not the vital effects, we elect to present previously described mechanisms and compare with previously published models for ¹³C, but not execute new model simulations to evaluate in detail the processes behind observations from individual new cultures. We have revised the discussion to more clearly compare the vital effects in coccoliths with the Δ₄₇ signal, and describe the interpretation of this comparison.
  (2) We have revised our conclusions that coccolith carbonate is precipitated in equilibrium. Both reviewers rightfully pointed out that it does indeed seem that coccoliths do not precipitate carbonate in equilibrium and disequilibrium effects are present. Instead we have reinterpreted our findings and suggest the use of our calibration for coccolith-specific carbonates. We also urge caution and discuss the interpretation of calcification temperatures for non-in situ biogenic carbonates, which can give highly variable interpretations of the same measured dataset.
  Our point-to-point responses are listed in blue as the following.
  
  Citation: https://doi.org/10.5194/egusphere-2023-2581-AC2

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

ED: Reconsider after major revisions (08 May 2024) by Luc Beaufort

AR by Alexander Clark on behalf of the Authors (08 May 2024) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (13 May 2024) by Luc Beaufort

RR by Anonymous Referee #2 (12 Jun 2024)

Suggestions for revision or reasons for rejection

Clark et al. extensively revised their manuscript and answered the reviewers' questions. They make a convincing case that there are no species-specific effects across the analyzed coccolithophores. However, there are still two minor points that the authors might want to consider.

1) The paper would still benefit from a brief, one-paragraph description of coccolithophore biomineralisation. The current sentence, beginning on line 74, merely references other papers without explaining the process. Providing this explanation is necessary to understand where vital effects could occur in coccolithophores.

2) The authors conclude that “[…] thus while we can’t fully rule out that vital effects are present on Δ47, the offset from the inorganic equilibrium calibration must be similar at all temperatures, systematic and unrelated to vital effects.” The authors do not make a convincing case for this. Specifically, they base their conclusion on considering only pH and growth-rate dependent kinetic fractionation effects as "vital effects" and observing no correlation between ∆47 and some calcification parameters. What about metabolic effects, diffusion, or crystal surface effects? The possibility of any of these factors provides a more plausible explanation for the observed offset between the coccolithophores and the other ∆47-T calibrations than suggesting that every other calibration is biased in some way.

Minor points:
Suggest removing “well-constrained” from the title. Although it may be true, this adjective unnecessarily lengthens the title without adding useful information.

L15: “We thus…” This sentence reads strange as it contains two clauses (thus, because) referring to why the authors chose coccolithophores. Consider rephrasing.

L31: It is confusing to highlight foraminifera here, as forms were not studied in the paper. Consider moving this statement to the outlook paragraph.

L34: Suggest removing “relatively new”. Ghosh et al. 2006 was a long time and over 200 clumped papers ago.

Chapter 2.2: did the different cleaning procedures affect the δ18O or ∆47 values?

Fig. 8: Consider explaining the difference between subplots a) and b) in the caption.

Hide

RR by Anonymous Referee #1 (20 Jun 2024)

Suggestions for revision or reasons for rejection

The authors have considerably revised the original manuscript, essentially overturing the study's conclusions and title. I would emphasize that this is not a problem in itself and actually shows a commendable willingness to reconsider one's initial interpretations. That being said, the manuscript still suffers from many problems, many of which are listed below in the line-by-line comments.

I see two major issues remaining at this point.

For one thing, the term "temperature calibration" would imply, to most readers at least, the absence of disequilibrium/vital effects on D47, or at least a quantitative scheme to correct these effects. This is not the case here. It is wrong to suggest that a "well-constrained" modern T-D47 relationship is a "calibration" (ie, has good predictive power) without explicitly demonstrating that the relationships applies equally well to different seawater chemistries. The authors do not explicitly make this claim, but point out repeatedly that their apparent D47 offset from equilibrium does not appear to vary (within precision limits, which is hard to quantify for the reader) with water chemistry, particularly pH or [CO2aq]. The range of pH investigated, however, is 8.0-8.7, which is clearly different from a Cenozoic range of 7.4-8.2 (Rae et al., 2021, Annual Review of Earth and Planetary Sciences). In my earlier review I called for explicitly listing the range of culture pH in the main text. In the revised manuscript, this information is provided but only in supplementary materials. Ultimately, in my opinion the authors do not convincingly argue that their culture observations are a good predictor of past coccolith D47-T relationships.

In other words: the revised manuscript appears to make the implicit statement that although we don't understand why cultured coccoliths have a different D47-T relationship from that observed in foraminifera, bivalves, slow-growing calcites, travertines, etc., this cultured coccolith calibration must apply equally well to all coccoliths, past and present. That is, again, a bold statement that calls for strong supporting evidence, that is simply missing at this point.

Second major issue: Despite the overturned conclusions, the manuscript still appears to promote the idea that all/most biogenic calcites follow D47-T relationships different from the equilibrium calibration (which is neither biogenic nor inorganic by nature, it's just thermodynamics). A very long section 4.5 appears to argue that point indirectly, essentially illustrating that calibration studies rest on many ambiguous interpretations, and that making somewhat arbitrary changes will yield a wide range of D47 "calibrations". In my opinion this is the weakest part of the manuscript, because it needlessly dives into arcane details and fails to make clear, compelling points. Ultimately, whatever the success of this argument, my previous review's point remains that if we are to conclude that most/all biogenic carbonates have out-of-equilibrium clumped isotopes, the logical consequence is that we need to understand the processes at play, because their isotopic effects are unlikely to vary only with temperature by default. Arguing for a universally applicable "biogenic" calibration is irrational and willingly ignores the well-established fact that biomineralization strategies are hugely variable across genera. In my opinion, the manuscript would greatly benefit if it stopped pushing this appealing but deeply misguided idea.

As it stands, regretfully I cannot recommend publication until these major issues are solved.

Line-by-line comments:

- Lines [25-26]: "agree with a previous culture study that there are no species- or genus-specific vital effects on the D47-temperature relationship in coccolithophores". As written, this is presented as a general truth.
- [32-33]: "All published biogenic studies fall within within ±1°C of our coccolith-specific calibration if [some arbitrary interpretative choice is made]". See my comments below regarding section 4.5.
- [65-63]: "However, there are clear discrepancies between most inorganic calibrations [...] and an often used, generalised biogenic calibration [Meinicke et al., 2020]": First, as written, this sentence suggests that there are discrepancies between the inarganic calibrations, which is arguably no longer the case. Ambiguity could be avoided by adding "on one hand" after the inoraginc references and "on the other" when citing Meinicke et al. Second, I'm not sure why Meinicke et al. is described as a "generalised biogenic calibration" since is is exclusively based on foraminifera.
- [fig 3] equilibrium and kinetic limit equations are switched.
- [349-351]: "This approximation is derived from their experimental setup, which is not necessarily in equilibrium, and therefore potential small growth rate and pH effects are still present". This statement is incorrect. This equilibrium limit is actually tied to the Devils Hole observation of Coplen (2007). Watkins et al. (2013, 2014) quite reasonably assumed that the T sensitivity of equilibrium oxygen-18 fractionation between calcite and water is inherited from that for DIC species, and assumption which was further strengthened by a second, later observation from Laghetto Basso (Daeron et al., 2019).
- [361]: The Daeron citation does not seem relevant here. Guo (2020, GCA "Kinetic clumped isotope fractionation in the DIC-H2O-CO2 system") might be more appropriate.
- [430-432]: "While the omni-variant generalised least squares regression would be better suited, as this incorporates the full error covariance (Daëron and Vermeesch, 2024), our data is standardised through reference materials in a moving time window and thus cannot be analysed through this method." Respectfully, may I suggest that this statement is irrelevant. As I noted in my earlier review, the temperature uncertainties are entirely negligible here, so that using York regression is already overkill. Using an even more complicated method is not warranted.
- [442-444] "All regression lines fall within 0.0012‰ error of each other, which shows that with the available data there is no species- or genus-specific vital effect on the Δ47-temperature relationship.". Again, I am compelled to point out that this statement is overreaching. For one thing, the fact that three regression lines (or rather, two regression lines and one isolated data point) lie within 1ppm of each other is one thing, but its significance depends quite a lot on the formal precision of the regression D47 values. If each of these lines had a D47 "precision" of 1 ppm, the agreement would be very strong, whereas for corresponding D47 precisions of 10 ppm, the statement would be much weaker. It would also be more fair to rephrase the second part of the sentence to "potential species- or genus-specific vital effects on the Δ47-temperature relationship remain undetectable at the X ppm level." (with X being the actual precision of the differences instead of the 0.0012‰ spread of regression lines).
- [455-456] "there is no carbon isotope vital effect affecting the coccolith Δ47-values"; [447-448] "an important impact of the oxygen isotope vital effect on coccolith Δ47-values."; [581-582] "The vital effects observed in the coccolith carbon and oxygen isotopes do not have an impact on the Δ47": This wording is quite confusing. 13C and 18O "vital effects" do not "affect" D47 values. Instead, isotopic disequilibria affecting different isotopologues reflect underlying physical and chemical causes.
- [459-462] "Thirdly, average Δ47 values were calculated for each species at every growth temperature. These temperature-weighted averages can highlight bias from a low number of measurement replicates at certain growth temperatures, such as at 6°C and 27°C. The resulting Δ47-temperature regression is indistinguishable from regressions using individual Δ47 sample datapoints ((±6.1 ppm; Table 2)." First, I don't understand. Are the regression not accounting for D47 uncertainties, which should scale with the inverse sqrt of the number of replicates? That would seem like the default method of performing such calibration regressions. Additionally, do I understand correctly that the quoted +/-6.1 ppm number is the difference between two different ways of performing the regressions? If so, that 6ppm difference seems quite large (equivalent to +/- 2 degrees) compared to the above statement that regressions agree to within 1.2 ppm.
- [492-493] "The biogenic data sets are combined into a general ‘biogenic’ calibration, excluding this study". This once again sweeps under the rug the fact that the two foram datasets were repeatedly shown to be consistent with one another, but published using different calcification temperature estimates, both of which are very likely flawed according to the reassessment of Daeron/Gray. What's more, Meinicke et al. (2020) also include many benthic foraminifera from Piasecki et al. (2019), which now appear to be either analytically compromised or far from equilibrium D47 values (cf Dearon & Gray, 2023).
- [497] "Daeron & Gray 2023 orig" is a misnomer. Both N. Meinicke and M. Peral have published I-CDES versions of their respective datasets, which should be properly cited.
- [fig 7] What is Daeron & Vermeesch ("MIT")? Is this a typo for Daeron & Gray ("MIT")?
- [499-519] I am truly sorry to say so, but with all due respect section 4.5 is neither a light nor a fun read. Juggling between original studies, the same studies recalculated with different T assumptions, partial versions of the same data by different authors, and datasets truncated below arbitrary T thresholds, yields a seemingly infinite number of semi-arbitrary options to chose from, detracting from the point(s) the authors' are trying to make. Is there something to be understood here beyond the fact that the cultured coccolith D47 values are greater than expected from non-coccolith calcite calibrations? If not, this can be stated much more simply. The section overall goes into bizarre tangents, such as a detailed critique of the earlier foraminifer studies, which I believe derails the discussion, only to conclude that "the use of calcification temperatures from oxygen isotopes need further testing, ideally on laboratory cultured specimens", a point that I believe is far from controversial today.
- [613-616] "Future studies with constrained and in situ temperature measurements such as in sediment traps (Clark et al., 2024) or cultures are recommended to disentangle and validate our findings of this biogenic disequilibrium." It would be misleading to suggest, as appears here, that "our findings of this biogenic disequilibrium" include non-coccolith biogenic carbonates. This is simply absent from this studies findings. Perhaps this is a remnant of the earlier version of the manuscript?
- [630-631] The revised conclusion states that "Our coccolith Δ47 data is largely consistent with a previous coccolith culture study (Katz et al., 2017), and indicates that coccolithophores precipitate coccolith calcite in clumped isotope disequilibrium". The original manuscript stated the opposite (clumped isotope equilibrium), but also claimed agreement with Katz et al. This highlights that the way(s) in which this study's results agree with those of Katz et al. are meant quite loosely (since direct I-CDES comparison remains impossible). I suggest that bringing up this highly flexible agreement does not truly strengthen the conclusion.
- [634-635] "The discrepancies derived from the differences in calcification temperature render it difficult to conclusively state whether a general biogenic calibration should be used": bringing this up in this way in the conclusion would require this point to have been explicitly and convincingly argued in the discussion, which is far from the case. Perhaps another remnant of the earlier version of the conclusions?

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ED: Publish subject to minor revisions (review by editor) (28 Jun 2024) by Luc Beaufort

Dear Authors,
Thank you for your revised manuscript and for addressing the reviewers' comments. After careful consideration of the second-round evaluations, I have decided to accept your article pending minor revisions. I will review these revisions myself once they are completed.
I ask that you follow the recommendations of both reviewers, particularly those related to the vital effects of coccolithophores. Specifically, please revise section 4.5 as it has been noted to be somewhat unclear and indirect. Additionally, it is essential to present your calibration in a more modest manner, clearly explaining that it is not a true calibration.
Reviewer 1 suggested including a brief description of coccolithophore biomineralization to help readers understand the context better. Additionally, they raised concerns about the possibility of vital effects that might not have been fully addressed in your current manuscript.
Reviewer 2 highlighted significant issues regarding the term "temperature calibration" and the implicit claims made about the applicability of your findings. They emphasized the need for strong supporting evidence to justify your conclusions and suggested that the current manuscript promotes an idea that may be misleading without proper context and clarification.
To summarize, please ensure the following revisions are made:
Add a brief, one-paragraph description of coccolithophore biomineralization as suggested by Reviewer 1.
Revise section 4.5 to be clearer and more concise, avoiding unnecessary complexity.
Present your calibration results in a more modest manner, explicitly stating that this is not a true calibration.
Address the points made by both reviewers concerning the vital effects and ensure your conclusions are well-supported by evidence.
Once these revisions are made, I will reassess the manuscript for final acceptance. Thank you for your cooperation and effort in improving the quality of your work.
Best regards,
Luc Beaufort

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AR by Alexander Clark on behalf of the Authors (07 Jul 2024) Author's response Author's tracked changes Manuscript

ED: Publish as is (10 Aug 2024) by Luc Beaufort

AR by Alexander Clark on behalf of the Authors (14 Aug 2024) Manuscript

Journal article(s) based on this preprint

20 Sep 2024

A clumped isotope calibration of coccoliths at well-constrained culture temperatures for marine temperature reconstructions

Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

Clim. Past, 20, 2081–2101, https://doi.org/10.5194/cp-20-2081-2024,https://doi.org/10.5194/cp-20-2081-2024, 2024

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Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

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https://doi.org/10.5194/egusphere-2023-2581-supplement

Alexander J. Clark, Ismael Torres-Romero, Madalina Jaggi, Stefano M. Bernasconi, and Heather M. Stoll

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Coccoliths are abundant in sediments across the world’s oceans yet it is difficult to apply traditional carbon or oxygen isotope methodologies for temperature reconstructions. We show that our well-constrained coccolith clumped isotope-temperature calibration falls within error of other biogenic carbonate calibrations, with a systematic offset to inorganic carbonate calibrations. We suggest the use of our well-constrained calibration for future biogenic carbonate temperature reconstructions.


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