The paper is very well written and it provides excellent observations that demonstrate that planktonic foraminiferal size normalized weight is highly variable among species, in different regions, and in response to different environmental variables. Results clearly demonstrate that size normalized should not be used as a pCO2 proxy. The paper is very well written, well organized and well-illustrated, and it merits publication and wide distribution among the research community. My edits are only minor grammatical corrections, and I have no concerns about the methodology, results, interpretations or conclusions.

This study by Barrett et al. examines the use of size-normalized weight (SNW) of planktic foraminifera shells as a proxy for reconstructing past environmental conditions, particularly seawater CO₂ levels (pCO₂). Using global data and Bayesian regression modeling, the authors find that no single environmental factor explains SNW variability across species and regions. Instead, species-specific and regionally variable responses suggest that cryptic species and phenotypic plasticity, such as changes in calcite thickness during reproduction, may influence shell weight. The study emphasizes the importance of regional calibration and careful species selection when using SNW as a pCO₂ proxy.

I find this study important and timely, as it effectively reminds the community that foraminifera shell weights are not an absolute indicator of seawater carbonate chemistry in the open ocean's natural conditions. However, I do have two major concerns about the study's methodology. First, although the authors, in their introduction and methodology, consider most of the factors that have been proposed over the years to explain variations in foraminifera shell weight, they do not account for recent studies that suggest changes in seawater density as a potential driver of these variations. I understand that seawater density and salinity may covary (in the surface ocean), but I still believe this factor is worth investigating. Second, the authors compare the SNW of deep-dwelling foraminifera species to surface ocean properties, which raises some concerns.

More specifically, Zarkogiannis et al. (2019) suggest that foraminifera utilize their shells for buoyancy regulation, adjusting their shell weight to maintain their position in the water column. In a subsequent study, Zarkogiannis et al. (2022) also discuss gametogenic calcite as a mechanism for buoyancy regulation. They observe that if foraminifera shell weights were primarily governed by CO₃^2- concentrations, deep-dwelling species residing in more acidic waters would exhibit the lightest shells. However, this is not the case. Their findings align with both the current study and that of Béjard et al. (2023), in which G. truncatulinoides, a deep-dwelling species, is observed to possess the heaviest shells. Moreover, Zarkogiannis et al. (2022) provide an additional 16 core-top samples that could be incorporated into the present study. As both CT and volumetric data are provided, size normalization to a linear dimension should be feasible.

My second concern pertains to the environmental data used for comparison with the SNWs. How surface were they? 0, 2,5, 5 or 10m? Additionally, do the authors believe that comparing surface ocean conditions with the SNWs of G. truncatulinoides, a species typically found at depths below 400 meters, is appropriate? What is the underlying assumption in comparing deep-dwelling individuals with surface ocean conditions? If not at bibliographic species-specific calcification depths, I would have expected to see at least a comparison with the averaged conditions between 0 and 100 meters depth, extracted from the models, to be used for comparison with the SNWs.

Furthermore, in a future submission please change planktic to planktonic. The correct adjective form of plankton is planktonic. The adjectives of Greek nouns ending in -on get the suffix -ic in the end like plankton – planktonic, bion – bionic, lacon – laconic. This is different to nouns ending in -os, which lose the ending -os to the previous consonant by replacing it with -ic, like bentos – benthic, cosmos – cosmic or chronos – chronic.

Minor

Line 27: Change “are a plankton” to “are a type of plankton.”

Line 62: What about seawater density?

Line 108: What are ecogroups? Consider mentioning the Aze et al. (2011) classification here, where ecogroups are first introduced. Are these ecogroups the same as those used in the group-level comparison? If so, why not refer to this comparison as ecogroup-level?

Lines 125-126: I think Marshall et al. (2013) should be cited here, as they introduced area density as a normalization method against silhouette area.

Line 150: Define ESMs at this point in the text.

Line 171: A reference for phosphate is missing.

Line 214: I am unsure if salinity is appropriate, as its depth profile varies with latitude. In the halocline (within the first 1000 m, relevant to foraminifera), salinity increases with depth at high latitudes but decreases with depth at low latitudes. Furthermore, there is a salinity inversion in subtropical regions. If SNWs followed the salinity profile of the water column in the subtropics, there would likely be a decline in SNWs with depth, but this is not observed.

Lines 247-248: This explanation belongs in the methods section. It is the first time that the rationale behind using ESM data is addressed.

Line 261: What happened to the merging of the 250–350 µm sieve fractions? It is unclear why the sieve fractions are separated in one instance and merged in another. Please clarify this point.

Lines 264-267: G. truncatulinoides has variants like excelsa, which are hardly differentiated, while de Vargas et al. (2001) and Quillévéré et al. (2013) identify four distinct types. Therefore, it is challenging to make assumptions based on data from a single study. Zarkogiannis et al. (2022) also present G. truncatulinoides shell weights, volumetric data for size normalization, and CT images for variant identification, which could be useful for the present study.

Line 281: The sentence appears incomplete; something seems to be missing at the end.

Line 345: Do you mean "ecogroup level"? If so, please revise for consistency.

Line 400: Is there any collinearity in the current dataset between CO32- and phosphate, as suggested by Marshall et al. (2013)?

Lines 433-436: Strongly agreed—nano X-ray tomography should indeed be considered.

Line 452: Also strongly agreed. However, I did not see any raw shell weights presented in this study. The Pangea links are missing.

One aspect not discussed in this section or elsewhere in the paper is the cleaning protocols used for foraminifera shell weight measurements in different studies. This aspect should eventually be standardized. As shown in the HyPerCal cleaning protocol, different treatments incorporate varying amounts of sedimentary contamination, which can affect SNW, particularly for specimens with large and multiple apertures, such as G. ruber plexus.

References

Béjard, T. M., Rigual-Hernández, A. S., Flores, J. A., Tarruella, J. P., Durrieu de Madron, X., Cacho, I., Haghipour, N., Hunter, A. and Sierro, F. J. (2023). "Calcification response of planktic foraminifera to environmental change in the western Mediterranean Sea during the industrial era." Biogeosciences 20(7): 1505-1528.

de Vargas, C., S. Renaud, H. Hilbrecht, and J. Pawlowski (2001). “Pleistocene adaptive radiation in Globorotalia truncatulinoides: Genetic, morphologic, and environmental evidence”, Paleobiology, 27(1), 104–125.

Marshall, B. J., Thunell, R. C., Henehan, M. J., Astor, Y. and Wejnert, K. E. (2013). "Planktonic foraminiferal area density as a proxy for carbonate ion concentration: A calibration study using the Cariaco Basin ocean time series." Paleoceanography 28(2): 363-376.

Quillévéré, F., R. Morard, G. Escarguel, C. J. Douady, Y. Ujiié, T. de Garidel-Thoron, and C. de Vargas (2013). “Global scale same-specimen morpho-genetic analysis of Truncorotalia truncatulinoides: A perspective on the morphological species concept in planktonic foraminifera”, Palaeogeogr. Palaeoclimatol. Palaeoecol.

Zarkogiannis, S. D., Antonarakou, A., Tripati, A., Kontakiotis, G., Mortyn, P. G., Drinia, H. and Greaves, M. (2019). "Influence of surface ocean density on planktonic foraminifera calcification." Scientific Reports 9(1): 533.

Zarkogiannis, S. D., Iwasaki, S., Rae, J. W. B., Schmidt, M. W., Mortyn, P. G., Kontakiotis, G., Hertzberg, J. E. and Rickaby, R. E. M. (2022). "Calcification, Dissolution and Test Properties of Modern Planktonic Foraminifera From the Central Atlantic Ocean." Frontiers in Marine Science 9.

I agree with the first two readers that this is an excellent, well-written manuscript that describes the results of a careful study that works to synthesize new and existing results.  The current state of the literature on shell normalized weight can be generously described as a confusing and contradictory, so this is a refreshing paper to read indeed.

I have four suggestions that I do think are important to incorporate to make this current contribution clear, in terms of its findings and implications and in allowing this study to be useful for future research.

1. Data and Code Availability: Like Reviewer 2, I went looking for the data and couldn’t find the raw data, something they explicitly implored other studies to make available. I suspect this is embargoed at present, but as a reviewer, this was unclear. Making the code available as well, would make this study truly replicable and should be done (and maybe the authors already have!).
2. Table of Statistical models and diagnostics: My apologies if I am missing this, but I was surprised not to see a table of the different models with diagnostics on relative model fit.  The authors describe their models in words, and some of the results, but do not provide a table of these models and results. It is fine if model results are included in the supplement only, but they should be included.
3. Handling and reporting of the fixed effect ‘sampling type’: Because I was involved in one study that found that the most important predictor of shell normalized weight was whether the test was from a sediment trap or core top, I was heartened to see this included as a fixed effect (and indeed, you discuss the literature regarding the potential importance of this factor).  I was thus confused as to why the importance of this condition was not reported, nor shown, in any of the figures.  I appreciate that you would want to consider the effect of this factor relative to other fixed effects, but to not report it at all nor show its effects seems like a missed opportunity.  Without knowing its relative importance, it is hard to know what to do with the results that a framed in terms of the conditions present in the surface ocean around the time that the individual was alive.  Here is where more information is needed on this fixed effect:
   1. Figure 1: symbol type could show whether the same was a trap or from the ocean bottom
   2. Results: please report the variance explained by the null model (i.e., fixed effects including sampling type). I assumed from the methods and from the use of the phrase ‘environment-only’ model that the reported model with 23% of variance explained excluded the sampling method fixed effect. Did the model with random effects include sampling method?  It is confusing without a table of model results to refer to (see pt #2).
   3. Figures: Please add this fixed-effect to Figure 2,3,4, so the effect and directionality of the effect can be understood.
   4. Discussion: given that the model includes this factor, you are in the position to discuss the relative importance (and overprinting) of diagenesis in the sediment versus conditions during life. I know that I, and a few others, would love to hear your thoughts on this, given the results—once presented!
4. Depth of Environmental factors: it is unclear from the methods (but could be clear in a data table) at what depth(s) environmental factors were extracted and considered from the models.  Were these all from the ‘sea surface’?  Are bottom water conditions considered for the sediment samples?  Are deeper depth conditions considered for those species that live at deeper depths?  Would this change the coherence and direction of results for those taxa?

If these general concerns could be addressed, as I suspect they might readily be, this will make an excellent contribution in my opinion!  I list a minor note below and I look forward to seeing the final version!

Minor: Line 170: change ‘inhibits’ to ‘inhibit’