the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 20 May 2026
Uncovering the Functional Roles of Plasma Membrane Proteins in Foraminiferal biocalcification
Abstract. The biocalcifying process in foraminifera, especially in benthic rotaliids like the Ammonia genus, involves intricate interactions between organic components and inorganic crystal formation, in which cellular membranes likely play a central but still underappreciated role.
We established a new extraction protocol enabling the isolation of membrane-associated and cytoplasmic proteins, as confirmed by proteomic analyses, revealing a clear spatial separation of protein functions. In particular, biochemical studies have identified an Annexin A13-like protein in membrane extracts of Ammonia spp. specimens, pointing to a conserved role for annexins in calcium regulation across diverse organisms, including these protists.
This study identifies membrane-associated proteins whose functions are likely linked to foraminiferal shell formation, potentially involving (i) annexin-mediated calcium transport at the site of biocalcification and (ii) regulation of ion flux through vesicle-based transport. Finally, we examined the Primary Organic Sheet (POS) using in situ carbon K-edge XANES spectroscopy on a focused ion beam (FIB) lamella from the final chamber of the Ammonia confertitesta test. The detection of lipid components suggests that this organic shell layer may partly derive from the plasma membrane, indicating its contribution to molecules forming the POS structure and composition.
Taken together, biochemical, proteomic, and ultrastructural evidence indicate that the plasma membrane, in addition to the well-established role of the shell organic layers, may play an active and sustained role in regulating foraminiferal biomineralization. These findings complete published models of foraminiferal biocalcification and support a framework in which the membrane and its associated proteins may represent central players in shell formation.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-2192', Marleen Stuhr, 29 Jun 2026
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RC2: 'Comment on egusphere-2026-2192', Anonymous Referee #2, 03 Jul 2026
This study characterizes the plasma-membrane proteome of the benthic foraminifer Ammonia spp. and attempts to link membrane-associated proteins to biocalcification, combining a new fractionation protocol, immunoblotting, nanoLC-MS proteomics, and in situ carbon K-edge XANES on the primary organic sheet (POS). The topic is timely and the fraction-resolved proteome of a rotaliid is a useful contribution.
However, the three central claims, a clean membrane/soluble separation, the identification of Annexin A13 as a calcification-related foraminiferal protein, and a plasma-membrane origin of the POS, are currently not validated, not corroborated by the authors’ own data, or over-interpreted from a single specimen. In addition, the bioinformatic methods are not reproducible as written and, as Table S1 confirms, the identifications rest almost entirely on cross-species homology. Please find below specific comments:
Introduction
L69. Please change “…to highlight their role in the biomineralization” to “…to highlight their role in biomineralization”.
L72. Please add a reference supporting “a family of Ca²⁺-dependent phospholipid-binding proteins known to regulate membrane-related processes and considered potential regulators of biomineralization.”
Materials and Methods
L90-93. Three species are named (A. confertitesta, A. parkinsoniana, A. tepida) but the text then refers to “These two species.” Please correct the count, and justify pooling the species as “Ammonia spp.”: the proteome is a multi-species pool, whereas the XANES is A. confertitesta only.
L100–116. The "membrane-associated" fraction is described as the detergent-solubilized material of a 14,000 × g pellet. A 14,000 × g spin does not sediment cellular membranes cleanly. Microsomal/plasma-membrane recovery conventionally requires ultracentrifugation (~100,000 × g), and differential centrifugation in any case yields only crudely enriched pellets that still contain mixed membrane populations (Graham 2015), so this is more accurately an insoluble-pellet proteome than a membrane fraction. Critically, the separation is not validated: no integral-membrane marker is shown to be enriched in the membrane fraction, and (more importantly) no cytosolic marker is shown to be absent from it, so contamination of the "membrane" fraction by soluble proteins is untested. Consistent with imperfect separation, Table S1 records extensive cross-fraction overlap (24 of 114 proteins are recorded in both the membrane and soluble/cytoplasmic fractions). Please (a) validate the fractionation with compartment markers, and (b) justify or revise the 14,000 × g scheme and the term "membrane-associated."
L161-167. “UniProt” (spelled “uniport” throughout, including in the URL) spans all of life, so a download date alone does not define the search space. Please state the taxonomic restriction applied, whether Swiss-Prot only or Swiss-Prot + TrEMBL, and the total number of entries searched. This is decisive for a non-model calcifier: as Table S1 shows, ~82% of identifications are matched to Reticulomyxa filosa (a naked, non-calcifying foraminifer) and only one to Ammonia itself, so essentially the entire functional interpretation rests on cross-species homology. This limitation must be stated explicitly and the interpretation limited to what homology-based identifications can support. Please also clarify what “a particular focus on foraminiferal protein entries” means exactly (a search restricted to foraminiferal/Rhizarian entries, or a whole-UniProt search with foraminiferal hits retained afterwards).
L163. The text describes a “de novo” approach, but de novo sequencing does not use a database, whereas a UniProt database was clearly used. PEAKS typically performs de novo–assisted database searching (PEAKS DB); please clarify which workflow was run and report the parameters for whichever mode generated the reported list.
L166-167. Please report the number of missed cleavages allowed, whether a contaminant database (e.g. cRAP) was included, and both the level at which the <1% FDR was applied (PSM/peptide, protein, or both) and how it was estimated (e.g. target-decoy). The FDR is currently asserted without a method. Please also state how trypsin-autolysis and human-derived peptides were filtered, with an all-of-life search and sparse foraminiferal coverage, false attribution of contaminant/human sequences to the target organism is a real risk (only keratins and single-peptide proteins are currently excluded).
L169-184. The XANES/TEM characterization rests on a single FIB lamella from the final chamber of one A. confertitesta specimen. Please state this sampling explicitly as a limitation on generality; it bears directly on the strength of the POS conclusions in Sections 3.3, 4.3 and 5 (see below).
Results
L199. “Fig. 1a,b” should read “Fig. 1c.”
L200-201. Please describe the qualitative and quantitative patterns in more detail. Note that “quantitative” is not supported by the current presence/absence (“X”) scoring; either provide quantitative data (e.g. spectral counts/intensities) or remove the word.
L202-204. The Annexin A13 result, central to the manuscript, is supported by a single commercial anti-ANXA13 antibody (raised against a mammalian target) giving a ~36 kDa band, and no annexin appears anywhere in the nanoLC-MS list (Table S1). Antibody cross-reactivity in a divergent protist is a genuine specificity concern, and "~36 kDa, consistent with annexin" fits many proteins. Please confirm the band identity by MS (excise and sequence it) before stating that this "confirms for the first time the presence of annexin family proteins in foraminiferal extracts." Two further points. First, an anti-ANXA6 antibody (A14725) is listed in the Methods (L124) but its result is never shown; the blot in Fig. 1d is the anti-ANXA13 probe (~36 kDa). Since ANXA6 is a large "double-core" annexin (~68 kDa), its result cannot be inferred from the ~36 kDa band and should be reported separately. If the ANXA6 blot was not pursued, the antibody should be removed from the Methods. Second, the annexin annotation is anchored to UniProtKB X6LBI7 with the rationale of "documented presence in R. filosa" (L202), i.e. Reticulomyxa, a different (naked) genus. Please state the source organism of X6LBI7 explicitly and temper the Ammonia inference accordingly
L203. “Fig. 1c” should read “Fig. 1d.”
Fig. 1d / Fig. S1b. The blot lane order (T, T, P, S — two T lanes) differs from the gel (M, T, S, P). Please check for a labelling error and confirm which lanes are shown.
L214-225 (and Table 1). Much of Table 1 (ATP synthase, isocitrate dehydrogenase, aconitase, succinate-CoA ligase, dihydrolipoamide dehydrogenase, actins, tubulins; and in Table S1 the largest group is proteasome/autophagy/proteolysis) is housekeeping/metabolic machinery present in essentially any eukaryotic cell. Detecting these in a whole-cell extract is not evidence of a role in calcification. Please separate the biomineralization-specific interpretation from what is expected background of a whole-cell lysate.
L219-222. The GO classification underpins the functional interpretation, but the annotation pipeline (e.g. Blast2GO, InterProScan, UniProt-GOA) and the criteria for functional assignment (e-value / percent-identity thresholds for homology-based transfer) are not described. Please report these. In addition, Section 3.2 consists entirely of methodological detail and should be consolidated into Section 2.6. Section 2.6 requires “at least two unique peptides,” whereas Section 3.2 states that proteins identified by “only a single peptide” were excluded. Please state the criterion once, consistently, and specify unique vs razor/shared peptides.
L236-242. The interpretation of the POS as "lipid-dominated," and therefore membrane-derived, is not established by the spectra shown. A carboxylic (288.6 eV) plus aliphatic (287.5 eV) signature is not lipid-specific: acidic (Asp/Glu-rich) matrix proteins, precisely the class expected in a calcification organic matrix, are carboxyl-rich and would produce a comparable feature, and the aliphatic and aromatic (285 eV) peaks occur in amino-acid side chains as well as in lipids. The one protein-diagnostic feature, the amide carbonyl at ~288.2 eV (which the authors themselves assign in the EDTA residue, L244), lies only 0.4 eV from the carboxylic peak and would require quantitative deconvolution against reference spectra to be excluded; no such analysis is shown for the POS. The lipidic assignment should therefore be demonstrated affirmatively or substantially softened. This is important because prior characterizations of the foraminiferal POS and associated organic layers, including Sabbatini et al. (2014), cited by the authors at L371–373 as reporting N-glycoproteins and high-mannose glycans, describe a predominantly glycoproteinaceous/saccharidic matrix. The reinterpretation of the same layer as lipid-dominated needs to be reconciled explicitly with that evidence (the entrapment scenario at L374 is a reasonable start but is currently asserted rather than shown), rather than presented in parallel with it.
Discussion
L265. Please explain in 1-2 sentences why separating membrane-associated from soluble proteins is crucial for interpreting their potential involvement in biomineralization, so it is clear also to a non-specialist audience.
L280-287. The annexin interpretation should be softened consistent with the comment at L202–204: pending MS confirmation of the band and clarification of the X6LBI7 source organism, statements that annexins are present and functional in Ammonia biocalcification remain speculative and should be phrased as such.
L288-301. “Cytoplasmic” and “soluble” are used interchangeably for the same fraction; a whole-lysate soluble fraction is not purely cytoplasmic. Please adopt one of the two consistently and define it. More broadly, the section attributes coordinated calcification roles to proteins whose detection is expected in any cell lysate (see L214-225); please align the framing with the whole-cell nature of the extract and the homology-based annotation.
L363-377. The conclusion that the POS is “an organic layer likely derived at least in part from the plasma membrane” extends a single-lamella, spectrally ambiguous observation into a general mechanism, and is not reconciled with the author’s own cited evidence for a protein/glycoprotein/polysaccharide matrix (Sabbatini et al. 2014; Weiner & Addadi 1997). Please either substantially soften this to a hypothesis, add replication/independent support, or reconcile it explicitly with the glycoprotein/polysaccharide evidence.
Conclusions
L386. “the Primary Organic Sheet (POS) represents a vestige of the plasma membrane” is stated far more strongly than n = 1 plus an ambiguous carbon-speciation signature can support. Please reframe as a hypothesis.
L379-392. The Conclusions currently restate the three central claims at full strength. Please revise this section to align with the more cautious framing adopted elsewhere in the manuscript, particularly with respect to (i) the membrane-proteome interpretation, which remains provisional pending validation; (ii) the proposed role of annexins, which requires independent MS confirmation; and (iii) the origin of the POS signal, which should be presented as tentative pending additional replication and/or reframing.
Citation: https://doi.org/10.5194/egusphere-2026-2192-RC2
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- 1
Dear authors and editors,
I have now re-read the manuscript, and compared to some provious studies on foram proteomics. The presented study presents a proteomics-based investigation of foraminiferal biomineralization in the common benthic Ammonia spp. (two species combined), combining protein fractionation into membrane-associated and soluble fractions, Western blot validation of annexin family proteins, and STXM/XANES characterization of the primary organic sheet. The methodological development, particularly the fractionation protocol that separates membrane-associated from cytoplasmic proteins, represents a potentially valuable technical contribution to the field., andthe STXM analysis of the POS provides high-resolution in situ molecular characterization that meaningfully extends prior structural work.
However, as detailed below, I have major concerns regarding the study as it seems to have significant shortcomings in experimental design, statistical rigor (it seems to lack replication and stats entriely), interpretation of proteomic data, and citation of the existing literature that, in the current form, limit the strength of the conclusions.
1. Absence of biological replication renders proteomic conclusions unreliable:
The most fundamental limitation of the study is the apparent absence of biological replication. Based on the Methods, specimens were collected from a single sampling event at a single intertidal site in February 2024. The protein extraction appears to have been performed on one pooled sample per fraction (total, cytoplasmic, membrane-associated), with no indication of independent biological replicates. No statistical analysis is presented for the proteomic data. Form my perspective, for mass spectrometry-based proteomics, biological replication is not optional, but the minimum requirement for assessing whether detected proteins are consistently present rather than artefacts of extraction, contamination, or preparation. Without at least three independent biological replicates, it is impossible to determine whether the protein identifications are reproducible, to apply any form of statistical testing, or to make quantitative comparisons between fractions. The authors acknowledge that their analysis is qualitative, but this does not circumvent the need to demonstrate reproducibility of detection across independent samples. Hence, the authors are encouraged to: (i) provide clarity on the number of independent extractions performed, (ii) if replication was indeed absent, explicitly acknowledge this as a major limitation of the study, and (iii) refrain from drawing strong mechanistic conclusions from non-replicated proteomic data.
2. Detection of a protein does not establish its functional role in calcification:
Throughout the discussion, functional roles in biomineralization are inferred from the mere presence of proteins in the foraminiferal proteome (which btw is also always a holobiont proteome). This logical leap is is a stretch too far from the data. For example, the detection of Annexin A13 in the membrane-associated fraction is used to suggest a role in calcium-dependent vesicular trafficking during calcification, yet no experiment is presented that links annexin abundance, localization, or activity to the calcification process itself. The same reasoning is applied systematically throughout the discussion, where the presence of Hsp70, Hsp90, Rab GTPases, Na⁺/K⁺-ATPase, clathrin, and numerous metabolic enzymes is taken as evidence for their involvement in biocalcification. Many of these proteins are ubiquitous housekeeping proteins present in virtually all eukaryotic cells regardless of calcification status and may fulfil a variety of functions.
Establishing a functional link to calcification would require, at minimum, one of the following: (a) differential abundance between calcifying and non-calcifying conditions; (b) spatial co-localization with active calcification sites (e.g., by immunofluorescence or immuno-EM); or (c) functional perturbation (e.g., inhibition of a target protein with demonstrated impact on test formation). The authors briefly acknowledge this in their statement that "functional studies are required to directly test this still speculative hypothesis", but this caveat is not consistently applied throughout the text, where the language frequently implies functional roles as if they were established findings. Therefore, I strongly suggest to substantially revise the manuscript to consistently and explicitly distinguish between what was detected and what is hypothesized to function. Phrasing such as "consistent with a role in" or "may contribute to" should replace language that implies established function.
3. Prior large-scale foraminiferal proteomics studies are inadequately cited:
The literature review and citation practice in this manuscript are selective in ways that appear to disadvantage prior work. Although I am not feeling comfortable as a reviewer telling authors to include our studies, it cannot go unnoticed that our two large-scale quantitative proteomics studies on large benthic foraminifera (Stuhr et al. 2018, Scientific Reports; Stuhr et al. 2021, Oceans) are either not cited or are cited only in passing, despite the fact that the majority of proteins discussed in this manuscript as potentially novel foram proteins were already identified in those studies, and in some cases even discussed in the context of calcification and vesicular transport. A non-exhaustive comparison with the protein inventory from Stuhr et al. (2018) and Stuhr et al. (2021) reveals (check the supplementaries; all data is also deposited in proteomeXchange) that the following proteins from the current manuscript's Table 1 were detected in those prior studies: Tubulins (α and β): Identified and regulated in both Stuhr et al. (2018) and Stuhr et al. (2021); discussed in the context of cytoskeletal dynamics and intracellular transport; Actin isoforms: Identified and regulated in both prior studies; Heat Shock Proteins 70 and 90: Central regulated proteins in both studies; their roles in protein quality control under stress are discussed extensively; Polyubiquitin: Detected in Stuhr et al. (2018) as a regulated host protein; Clathrin heavy chain: Detected in Stuhr et al. (2018) and (2021); Na⁺/K⁺-ATPase and alpha-2 subunit: Detected in Stuhr et al. (2018) in the host (Reticulomyxa filosa-assigned cluster), and further examined in Stuhr et al. (2021); Rab2/RabB-family GTPase: Detected in Stuhr et al. (2018); Rab7: Detected in Stuhr et al. (2018) in the host compartment... this is in fact the protein already cited as "Stuhr et al. 2021" in Table 1 of the current manuscript, yet the 2018 study, where it was first reported in this organism, is not cited; 14-3-3-like protein: Detected in Stuhr et al. (2018); Isocitrate dehydrogenase, aconitase, succinate-CoA ligase, dihydrolipoamide dehydrogenase: All detected in Stuhr et al. (2018); Calponin homology domain-containing protein: Detected and regulated in Stuhr et al. (2018); Kinesin-like protein: Detected in Stuhr et al. (2018); Annexin VI (Annexin 6): Also detected in Stuhr et al. (2018) (Cluster 6, host-assigned Reticulomyxa sequence), though not prominently discussed.
Therefore, the claim that the current study provides "the first" characterization of several of these proteins or pathways in foraminifera is not always supported. So, the authors are asked to conduct a thorough review of these and other (see refs therein) prior studies and to appropriately cite them throughout the manuscript, including in the Introduction, in Table 1, and wherever specific protein families or pathways are discussed. Claims of novelty should be re-evaluated in light of prior work.
4. The fractionation approach is the genuine methodological contribution, so it should be presented as such:
The most defensible novel contribution of this study is the development of a protocol that isolates membrane-associated proteins from soluble proteins in a small number of foraminiferal specimens. This is a meaningful technical advance, as most prior foraminiferal proteomics work (including the studies above) used total protein extracts or shell organic matrix preparations. The fractionation approach has genuine potential for addressing questions about the subcellular localization of proteins. From my perspective, this contribution is currently obscured by over-interpretation of the proteomic data and by novelty claims that do not hold up against the existing literature. The authors are encouraged to restructure the draft to foreground the fractionation protocol as the central contribution, and to frame the protein identifications, including the annexin finding, as hypothesis-generating observations that motivate future targeted experiments, rather than as evidence of specific functional roles.
5. XANES-based interpretation of the POS origin should be framed as a hypothesis:
The STXM/XANES analysis is technically sound and represents a genuinely informative dataset. The spectral signatures of the POS seem correctly described as consistent with lipidic compounds. The interpretation that this signature reflects a plasma membrane-derived origin for the POS is an interesting and testable hypothesis. Nevertheless, the current discussion sometimes presents this interpretation as if it were established: for example, "we propose that the POS represents an organic layer likely derived at least in part from the plasma membrane" appears in the discussion as a fairly firm conclusion, while later the authors acknowledge it as a hypothesis. The spectral data are consistent with a lipid-rich composition but cannot definitively distinguish plasma membrane origin from, for example, intracellular membrane remnants or secreted lipoproteins. This should be more clearly acknowledged.
Minor comments:
- The 90 μm sieve for removing juveniles is described as separating "adult specimens," but the developmental stage of individuals post-sieving is not confirmed by any measurement. This should be stated more carefully.
- The number of specimens used for Western blot (200) versus mass spectrometry (500) differs substantially. The impact of this on relative protein representation between fractions should be briefly addressed.
- The discussion references Prada et al. (2024) extensively as a precedent for the proteomic framework, but this relationship should be described more precisely: is the present study replicating that framework, extending it, or comparing results... ? If it is used so excessively, it would be helpful to have more insights from that work than the one sentence in the intro.
-The introduction states that "targeted proteomic analyses were performed", but I am not sure I understand what is meant by this. Targeted proteomics usually involve something like label-based quantitation of specific proteins, which is not describe in the methods (but might be an interesting approach to consider).
- L103: what kind of eppendorff tubes were used? With such small amounts of proteins I highly recommend protein LoBind tubes, especially since some proteins may preferentially bind to the tube, getting underrepresented.
- L106: which protease inhibitor cocktail was used? where was it purchased from? For such delicate techniques, all relevant materials and chemicals must be named with provider and country of origin (other missing below).
- L195-196: this reads as if the bubble formation is intended and improving the protocol, although I assume the opposite is the case. Please clarify,
- L202: spell genus name in full at first menion
-L220f: what were the thresholds and specifications for the database search, the reference taxa?
-L231: please write abbreviations in full at first mention, and what do you mean by foraminiferal walls? Cell walls? shells?
- Sometime (e.g. L335, L362) functional implication statements do not have any references, which would strengthen your interpretation.
Overall, the study addresses an important question, the molecular underpinning of foraminiferal biocalcification, and contains technically solid components, particularly the STXM characterization and the membrane fractionation protocol. With substantial revision to address the replication issue, the functional interpretation of proteomic data, and the positioning relative to prior literature, the study could make a meaningful contribution.
I am happy to see more proteomic studies appearing in foraminiferal research and would like to encourage more studies in that direction. Hence, I hope my comments and suggestions will not demotivate the authors but be perceived as constructive to strengthen the final outcome of the study and move the field forward. I am happy to receive specific questions.