We thank reviewer 1 for their time and very helpful guidance. Please see AC1 for the initial reply.

Final responses to Reviewer 1:

The authors have carried out the new analyses as suggested by Reviewer 1, some of which is reported on in document AC1.  This has resulted in a much larger dataset after filtering (1548 ASVs compared to 130 ASVs). As a result, we now address below those comments that remain relevant to the new dataset.

Comments:

1. The authors performed differential expression analyses using DESeq2. However they do not clarify whether they used pre-processed data or the raw read counts as input for the function, as recommended by the algorithm's developers [2], [3].

We carried out DESeq2 analysis on the raw counts as recommended, this has now been clarified in the manuscript. We thank the reviewer for highlighting the omission. The analysis has been re-done given the new dataset, with analysis both at the individual ASV level and amalgamated at the genus level. Also, we have carried out this analysis excluding foraminiferal samples that were taken from stations where we have no water data (as suggested by the reviewer in point 2 below). We also re-did the analysis on the station 101 dataset where we have a more robust number of foraminiferal samples.

1. The results of the permutational multivariate analysis of variance presented on line 273 (page 13) show that location explains 49% of the variability in the ASV profile of  pachyderma. This means that almost half of the observed differences in the microbiome composition among the 28 specimens can be attributed to the different sampling locations. In light of this significant effect of sampling location, the authors should refrain from including the 17 specimens with no contextual seawater samples (Stations 176, BB2, 129, 301) in the differential expression analyses.

We have redone this analysis, using our robust Aitchison clt distances and PERMANOVA, Adonis (qiime2) and have also used manyglm from mvabund to look at the statistical differences of this larger dataset which now contains 1548 rather than 130 ASVs.

We tested the null hypothesis that there was no significant difference in the water samples from the three stations, and also the null hypothesis that there were no differences in the ASV compositions with depth. The results from the PERMANOVA (Adonis) show that station only drives 2.34% of the variation, but that this is non-significant (Pr=0.063). However, mvabund (manyglm negative binomial model) shows marginal significance for “Station” (LRT=1319, P<0.035). “Depth” is the significant driver in differences in the water column.

We tested the null hypothesis that there are no significant differences in the ASV composition between the two provenances in (i) the entire dataset, (ii) the dataset (forams and water) from stations 101, 115 and 323, (iii) 101 only (due to the more robust numbers of foraminifera for statistical analysis). In all cases a significant difference was returned by at least one of the tests. We have tabulated our results for the revised manuscript, as requested by the reviewer.

1. In lines 261-266, the authors state that a differential expression analysis was repeated with a subset of foraminifera and water samples from station 101 to control for the effect of geographic location, claiming that the results are consistent with those presented in Fig. 4. The results of this control test are reported in Fig. A3 (page 30).

However, upon comparing the plots, it becomes evident that the results are dissimilar and partially contradict those reported in Fig. 4:

• The taxa Flavobacteriaceae and Crocinitomix are more expressed in the foraminifera samples in Fig. 4 but more expressed in water samples in Fig. A3.
• The taxa Chaetoceros, Bradyrhizobium, Moritella, Synedra, and Rubripirellula (among others) are not found in the differential abundance analysis presented in Fig. A3.

These inconsistencies indicate the significant influence that the selection of samples included in the differential abundance analyses can have on the results.

Some of the confusion here, lies in the agglomerating of ASVs at the Genus level for the figure, and for example the Flavobacteriaceae highlighted are not the same ASVs. This is something we should have raised and thank the reviewer for pointing it out. When presenting the new dataset, we will be clearer in highlighting the similarities and differences we observe. As mentioned above we have now carried out DESeq2 analysis on two datasets: (i) excluding forams for which there is no water sample to compare, and (ii)  station 101, both with the new much larger dataset of ASVs. Looking at all water stations, there are 13 significantly more abundant ASVs in the foraminifera, and 14 at station 101. Ten of these are the same ASV in both datasets. We have also carried out the analysis on data agglomerated to the genus level to reduce the number of features and the noise associated with individual ASVs. This also improves the statistical power of DESeq2 as it increases the counts per group. This highlights a much larger number of ASVs (or rather genera, 51) with increased abundance in the foraminifera. We will discuss this dataset and highlight differences between station 101 alone, and the larger dataset containing all three stations.

1. Given the relevance of the surrounding community in determining interactions with the foraminifera (line 273, page 13), the authors should be more cautious in their interpretation of their results. A thorough ecological discussion on the prokaryotic community in the water column samples, taking into account the environmental parameters measured, should be included given the importance of geographic location before speculating on the potential role of a given taxon as part of the  pachydermacore microbiome.

For example, the authors could consider including the time since the ice break-up in their analysis to provide ecological context to the prokaryotic community, which is dominated by Bacteroidetes and Proteobacteria in particulate organic matter in sea ice and sinking particles under the ice [4].

As reported under point 2 above, in our new analyses we have shown that “Station” drives 2.3% of the differences in ASV composition (rather than 49%), and is not significant (PERMANOVA, Adonis). However, the manyglm binomial model analysis (mvabund) demonstrates marginal significance of this factor. Both analyses, however, do indicate that the provenances “foraminifera” and “water column” are significantly different. Here then, we have been able to reject the null hypothesis that there were no differences in the ASV compositions between “Provenances” and accept the null hypothesis that there are no differences between “Station”, indicating Provenance rather than Station (location) has more influence on the ASV composition. We have changed the section of the manuscript referred to above to reflect this new data, but still agree with the reviewer that we should be cautious in interpreting our results, particularly given the “snap-shot in time” nature of the water samples in particular. In light of this, we will provide more cautious interpretation of the ASVs that make up the core microbiome, and interestingly, despite the new total of 1548 ASVs, the core microbiome remains unchanged. Indeed, our water column data shows a very significant difference between the water column ASV composition across the water depths, and since we unfortunately do not have depth data for our foraminiferal samples which were collected via a 200m haul, a full discussion of the water column composition at each depth in relation to the foraminiferal microbiome is not possible with this dataset.

Whilst we recognize the importance of geographic location and environmental parameters in shaping these interactions, including an in-depth discussion on the prokaryotic community and factors such as the time since ice break-up would require a significant expansion of our study's scope and objectives. We have aimed to provide a focused analysis on the foraminiferal core microbiome, acknowledging the broader ecological context where relevant. We agree that future studies could benefit from a detailed ecological perspective, and we will certainly consider this in our subsequent research efforts.

1. Line 435 The authors briefly mention the potential differences in the core microbiome or diet at different ontological stages. Since no data is presented on the size of the specimens analysed this aspect should be discussed.

We can add a sentence to discuss this further. For example, there is a suggestion that the diet of N. pachyderma changes between juvenile and adult, and it has been observed that gametogenic specimens stop eating.

1. Lines 422-424 (page 20): The authors do not present any evidence beyond the low ASV richness to support the classification of specimens Fm176b and Fm101e as gametogenic. Other potential explanations for this pattern should be discussed.

In response to this and other comments, and to the larger dataset we now have available, this sentence has been removed from the manuscript.                                                                                                                                

Technical corrections:

1. The datasets, the ASV sequences utilized for the analyses, including the code should be made accessible in public repositories to ensure the reproducibility of the results.

The raw data is publicly available a NCBI (BioProject accession PRJNA984332). The ASVs utilised in the study can be put on Figshare, for example, with a permanent DOI. The code used for this analysis is not custom code, written by the authors. We have provided all the details of each package utilised where code for all the functions used can be found.

1. Station 60 is mentioned in Table 1 but not plotted in Map in Fig. 1 nor mentioned in the text.

Our apologies, this shall be rectified

1. Lines 243-244 should be moved to the methods section

The authors are a bit unclear about what exactly should be moved within these lines.

1. The conclusion section is missing

Again, our apologies. This is rectified in the updated manuscript.

1. Line 819 correct reference format; Greco et al 2021 is cited in the text but not present in the reference list; Greco et al 2019 reported twice in the reference list

All references will be checked, thanks to the reviewer for spotting these.

Response to reviewer 2

General comments from the Authors

We thank reviewer 2 for taking time to review our manuscript, and, in particular, for taking great care to flag even small, but important errors. We are very grateful to them. One of reviewer 2’s great concerns is the lack of evidence in the TEM imaging for a role of kleptoplasty for diatom chloroplasts in N. pachyderma. We want to stress from the start that we are not asserting that the chloroplasts observed in TEM and those identified through 16S metabarcoding, are kleptoplasts in the traditional sense of the word. We have no data to support photosynthesis by the chloroplasts, or of the stability of the chloroplasts in the N. pachyderma cell. We had hoped that we had made this very clear in the manuscript, but reading the comments of reviewer 2, we conclude that there is room for an even clearer stance on this, and we will edit the manuscript accordingly.

We believe that this dataset provides some new and important information that should be available to the foraminiferal/plankton scientific community. Given the often-opportunistic nature of sampling in Polar regions, providing this information enables new framing of questions about N. pachyderma in Arctic waters, and the right experiments to be carried out to answer them, by whomever has the opportunity to do so.

Major points:

• As written, the rationale for this study is compelling (lines 90-94)—the species is important to the Arctic, which is a rapidly changing habitat due to global warming.  That passage is a bit misleading, however, as it notes the data presented here directly impacts understanding of trophic interactions, seasonal shell geochemistry, population dynamics modeling, carbonate flux, and evolutionary pressures. While insights can be gleaned about trophic interactions and – perhaps—evolutionary pressures, the sampling was not done seasonally, so little to nothing can be asserted about carbonate geochemistry, carbonate flux, and population dynamics. 

We accept Reviewer 2’s point that our data set does not directly address understanding of seasonality, population and carbon flux, although we do believe it is useful in providing additional data to existing literature. We will therefore amend lines 90-94 to focus more on trophic interactions and evolutionary adaptations.

However, in terms of the geochemical significance, we believe that if the chloroplasts are in future confirmed to be photosynthesizing inside the foraminifera, their presence will have implications for shell isotopic ratios as observed in species that host photosynthesising symbionts. It is therefore imperative that we communicate this finding so that the scientific community can research the role of these chloroplasts and their impact on the host. Is this an adaptation that has led to the success of this species in the Arctic, and does it impact shell chemistry and therefore affect the palaeorecord?

• Overall, the contribution is mostly well written and mostly logical.  There are, surprisingly, considerable errors in mechanics and grammar, as well as minor points, which are listed separately, below these more-substantial points.   

We thank the reviewer very much for taking the time to point out the grammatical errors, which we will correct and double check.

• pachydermais touted as a polar / high-latitude taxon, yet lines 592-593 indicate it also occurs in the tropics. This contradiction should be explained a bit more thoroughly in the context of impact to high (or low) latitudes.

We will add the biogeography of N. pachyderma in more detail. It is predominantly a high latitude species, but genotypes also occur in cool upwelling waters in the lower latitudes such as in tropical upwelling in the Arabian Sea and the Eastern Boundary Upwelling Currents off Namibia. It is, as yet, unknown whether these N. pachyderma types also contain large numbers of chloroplasts.

• It is rather unfortunate that the samples for DNA barcoding were collected in a different year and region from those collected for cellular ultrastructural analysis (TEM). How do the authors truly know that the TEM results (collected in 2018) are representative / comparable to sequencing results from populations collected in 2017? 

We agree that there would have been several advantages to having parallel samples from each sampling station on which metabarcoding could have been carried out alongside TEM. As stressed by the reviewer this would have enabled a strong case to state that the two datasets were representative/comparable with one another. Unfortunately, this is not the dataset we have, given the opportunistic nature of the samples available for these analyses.

To avoid any confusion, we have specifically taken them as stand-alone projects. The TEM images highlight large numbers of chloroplasts within N. pachyderma, which to our knowledge has never been reported before. In our manuscript we highlight that the limited preservation does not allow us to unequivocally state that these chloroplasts are from a diatom source.

For the 16S metabarcoding on average 55.7% of ASVs come from chloroplasts and this data therefore supports the observations in the TEM. In 16S metabarcoding we can also state that most chloroplast sequences come from diatom chloroplasts, (52.7% from diatoms specifically) concluding that N. pachyderma samples cross Northern Baffin Bay at the time of sampling contain a high proportion of diatom chloroplasts compared to other chloroplasts/bacteria.

One advantage of having samples from different temporal and spatial scales is that we demonstrate, using these two methods, that chloroplasts are found in high numbers in N. pachyderma in the summer months across large spatial scales within the Bay and in consecutive years, and it is not therefore just a snapshot in time or space.

• Given the assertion of phototrophy (line 544), a short passage should discuss light levels at the sample sites and water depths in different parts of the year, with literature citations.  Are other N. pachyderma known to photosynthesize?

In line 544 we are not asserting that N. pachyderma is kleptoplastic, but that given the significance of this adaptation to other protists, it is very important to confirm the nature of the chloroplast-foram relationship in this species going forward. We will more strongly emphasise this distinction. Now that this work has revealed the presence of large numbers of chloroplasts, we are recommending further studies to understand the role of these chloroplasts in the survival of N. pachyderma. We know those benthic foram species that eat diatoms, but are not kleptoplastic, do not contain so many chloroplasts in their cytoplasm (see lines 549-556 for this discussion) so the question here is why do we see so many? We aim to discuss the various possibilities in this manuscript to enable other scientists who may have opportunity to collect samples from the Arctic, to test these hypotheses.

No planktonic foraminifera have yet been proven to be kleptoplastic, and this would be the only means by which N. pachyderma could photosynthesize. We recommend investigation of other N. pachyderma genotypes to investigate whether this is an Arctic adaptation, or a more widely held adaptation across different biogeographies/genotypes, as discussed at lines 590-596.

• Lines 87-90 state that 16S rDNA is used here to determine prokaryotic biotic and trophic interactions, and potential symbiotic associations with TEM utilized to note ultrastructural attributes.  It is not clear how these methods can be used to inform that these observed chloroplasts are of diatom origin. More specifically, how can ASVs be assigned to diatoms (eukaryotes) from 16S rDNA sequence data (e.g., lines 224-229, Fig. 3)?  How were chloroplast ASVs assigned to diatoms (Fig 4, line 252)?  While my molecular colleagues and one publication (Bonfantine et al 2021 PeerJ) more-or-less explained how this might work, it might be wise of the authors to explain more precisely how they performed these analyses. 

Our TEM images demonstrate chloroplasts, and as mentioned above, in lines 355-368 we highlight some diatom chloroplast characteristics that can be identified, and others that unfortunately cannot, given the fixation preservation level achieved here.

16S ASVs can be assigned to chloroplasts from specific genera because the chloroplasts contain 16S genes in their genomes, given their considered evolutionary root as alphaproteobacteria. These 16S sequences are divergent enough to identify the chloroplast source. Chloroplast 16S sequences from known species, alongside bacterial sequences are part of the SILVA database used to assign taxonomy to the ASVs produced in this study.

We would be happy to include a few sentences on these analyses.

• Why doesn’t the ASV noted on line 301 align as Chaetoceros?  There are other Chaetoceros in Fig. 5.  Why the inconsistency?   Why doesn’t Fig. 6 show Chaetoceros gelidus while it shows the other common diatom, Fragilariopsis?

The SILVA database used to assign taxonomy to the ASVs clearly identified some ASVs as Chaetoceros but was unable to identify ASV15 beyond the class level. This is likely because ASV15 was more divergent from the Chaetoceros sequences in the SILVA database. It is common practice to further investigate key ASVs, such as ASV15, by a BLAST search against additional databases, to confirm or indeed, get better taxonomic resolution of sequence information. We performed this analysis, to confirm ASV15 was a Bacillariophyceae and more specifically could be identified as a Chaetoceros.

In Figure 5, the data is based on taxonomic assignment of ASVs against the SILVA database, so ASV15 is grouped alone as a Bacillariophyceae. This therefore gives a clear illustration of the relative abundance of this single ASV. We can make this much clearer in the manuscript and appreciate this being flagged by the reviewer.

Figure 6: 30.3% is ASV15, and should be labelled Chaetoceros (Bacillariophyceae), given the BLAST identification, this is an error and will be corrected.

• Another aspect of the contribution is also confusing in that most of the Introduction, Results, and early Discussion focus on trophic aspects (i.e., food and diet) while the last part of the Discussion focuses on kleptoplasty.  It was refreshing to see that TEM was performed for this contribution because it is perhaps the best way to document a putative kleptoplasty. Unfortunately, the TEM images presented were not convincing for a few reasons (noted below). More TEM images are required for review.  If the authors can firmly justify this taxon is kleptoplastidic, then the results should be written in this context.  If such justification is not possible, then the authors should consider altering those kleptoplasty passages to reflect phagotrophy and digestion.  Further, the ultimate conclusion that N. pachyderma is a mixotroph and kleptoplastidic is rather a leap from TEM analysis of specimens collected once in the summer.  At the very least, structural documentation should be obtained to show plastid degradation in winter or very early spring (to account for digestion / mixotrophy). While such collections are likely out of the question, the authors should address these shortfalls in the Discussion.

We are sorry that the reviewer found this format confusing. Our aim was to investigate the feeding behaviour of N. pachyderma, and to assess any potential symbionts (TEM can help to assess living microorganisms versus food). Therefore, our focus has been to report the 16S assemblage in the context of food and diet, and finish with a discussion on the chloroplasts and their potential role - one of which could be as photosynthesising kleptoplasts.

We believe that we have addressed the shortfalls of our TEM fixation preservation in the manuscript (lines 363-368) but are happy to be more forceful on this, since we agree with the reviewer here. Because our data cannot yet confirm kleptoplasty, we have discussed a range of potential roles of the chloroplasts. The first section discussing the chloroplasts (4.4) expands on evidence for and against a kleptoplastic role (both traditional photosynthetic and non-traditional) bringing in information from other studies. We believe this is fully justified, as kleptoplasty is one possible, and significant role that could be played by the chloroplasts.  However, there is also discussion of the nutritional value of chloroplasts in lines 599 to 604, and the benefits of storing or very slowly digesting them for overwintering success. We believe that these two sections (4.4 and 4.5) do cover the alternative roles (phagotrophy and digestion) as requested by the reviewer. The text can be modified however, to give a more equal weighting to each of these possible roles.

• Figure 7 is adequate documentation of potential kleptoplasty ONLY if additional higher-magnification images are included. It is imperative to be able to clearly examine some individual chloroplasts to determine if they are intact or in degraded state. Also, foraminiferal viability is typically determined by status of mitochondria (e.g., LeKieffre et al 2018 Mar. Micropaleo.; Nomaki et al 2016; Bernhard et al 2010), none of which are shown in this figure / contribution. Lipids should not be black, as shown in panel d. 

As per previous responses, the preservation of our foraminiferal samples for TEM was variable and was not of high enough quality to support or refute kleptoplasty. The TEM images are therefore presented only as a means of demonstrating the uniquely large numbers of chloroplasts within the foraminiferal samples, which itself has never been reported in planktonic foraminifera. This will be made clearer in the manuscript - see previous responses on this issue. Lipids in several foraminifera publications appear very dark grey/black, for e.g.  https://doi.org/10.1093/femsec/fiz046 https://doi.org/10.1111/1462-2920.14433 and LeKieffre et al. 2018b already cited, but we now recognise that our “lipids” appear much darker, and therefore we will remove the labelling.

• TEM images provided in Fig. A6 are equally too low in magnification to be very helpful in the context of documenting kleptoplasty.  It appears that the images in panels f, g, and h have degraded chloroplasts (i.e., evidence of phagotrophy rather than kleptoplasty).  Organelles in Panels b and c are difficult to identify at all (very low magnification). 

As previously mentioned, the preservation in our fixation was limited and we therefore cannot conclude anything from the state of degradation in the chloroplasts. These TEM images are provided to demonstrate the presence of chloroplasts found in our specimens, and not to support the hypothesis that the chloroplasts are traditional kleptoplasts. We will make this clearer.

• More specifically regarding Fig. 7, there is no scale bar in b; the scale in d cannot be correct (caption states bar is 1 micron but that would make those lipids and plastids all far less than 1 um, which is highly atypical; scale in e has no length assigned; panel e should be oriented as it appears in panel c (c has box outlining panel e). Panel b mostly shows the exterior (if one believes the caption); it is not clear why that image was selected as it barely shows N. pachyderma cytology. Fig 7 caption is unclear in places (“pore shape” noted for panel a—presumably intended as “cross section of pore plugs and inner organic lining”?).Further, panel b lacks any “f” label (see caption).   

We will review the figure legend and aim at improving clarity. We can state at the beginning of the legend that the TEM images show the large numbers of chloroplasts inside N. pachyderma, but do not confirm kleptoplasty. This figure would benefit from being a full page, rather than half a page.

Figure 7 panel a. We thank the reviewer for the suggested labelling of the pore plug – we will change this, as their suggestion is much better!

Figure 7 panel b external to the foram has been shown because it gives some interesting context. It does show a small number of internal chloroplasts and shows that the surrounding POM is stable and contains empty diatom frustules. The scale bar is present in the bottom left corner, as in panel a, but now the reviewer has flagged this, we can see that it is difficult to discern. We can make this more obvious. The “f” is also present, but in white, and we will also modify this for clarity.

Figure 7 panel d and e. The scale bars are 2 microns.

Panel c/e we will sort the orientation.

• Greco et al. (2021) is cited often (e.g., line 61, 82, 85, 396, 413, 443, 457, 481, 533, 588, 612), yet that reference does not appear in Reference list.  It is rather unfair to the reviewer and reader that a paper is cited >10 times but details of publication are not given. 

Our sincere apologies for this. It will be rectified.

Reviewer Minor but important points:

• The title does not indicate the report is on a planktic foraminifer. 

We will insert the word planktonic into the title.

“The 16S rDNA microbiome of the Arctic planktonic foraminifera Neogloboquadrina pachyderma is comprised of hydrocarbon-degrading bacteria and a diatom chloroplast store.”

• Line 321 is arguable because the two foraminifera could have phagocytosed while at a given water depth and then migrated vertically to another layer / depth horizon. 

The reviewer is correct, N. pachyderma migrates through the water column, over its life cycle with juveniles being found at the surface and more mature specimens being found below 50m-200m in general. If the chloroplasts are stored for any length of time therefore, the prey may have been phagocytosed in the upper water column, prior to the foraminifera descending as it matured. If the chloroplasts are rapidly digested however, this would not hold true, as foraminifera do not vertically migrate over diurnal periods of time (e.g. Meilland et al., 2019 https://doi.org/10.1093/plankt/fbz002; Manno  & Pavlov 2014, DOI 10.1007/s10750-013-1669-4). We are happy to omit line 321.

• Please use the proper term for the hard parts of foraminifera: “tests”, instead of “shells” which is used throughout the document. 

We chose to use the term “shell” rather than “test” as the word “test” has other meanings in English, and “shell” has been used in many manuscripts. However, we are happy to comply with the reviewer’s request and use the term “test” instead.

• Line 43: please be more specific about “within a short time frame”.

We can change “within a short time” to “ice free as early as 2030, and by 2055” and include additional references to support this; Jahn et al 2024 https://www.nature.com/articles/s43017-023-00515-9 and Kim et al. 2023 https://www.nature.com/articles/s41467-023-38511-8).  

• Iine 53: omit “habitat”.

Ok.

• Beginning of sentence spanning lines 71-73 is awkward (“Metabarcoding investigations of other taxa within the Neogloboquadrina genus…”).  Why not simply “Microbiome metabarcoding of Neogloboquadrina species…”?

We agree and this will be changed.

• Line 112: a colon should replace the semicolon.

OK

• Line 116-117: what is “salt adjusted phosphate buffered saline”?  First, “salt adjusted” should likely be hyphenated.  Second, what salt(s) is adjusted and from what concentration to ending concentration?

We will hyphenate this. Marine or salt-adjusted PBS is modified to match the salinity of the marine environment from which the samples were taken, to prevent osmotic stress and bursting of cells. Salt was added to the PBS to account for the marine conditions. For 35ppt, NaCl is added to PBS at 24.62g/l. We will add this information.

• Line 142: presumably need to insert comma after parenthetic.

Ok

• Line 174: Shouldn’t “faith pd” be capitalized to read “Faith PD” or “Faith Phylogenetic Diversity”?

Yes, this will be corrected.

• Line 193 requires comma after assemblages. Omit comma after “differences” in line 195. Line 203: insert comma after parenthetic.

Ok

• Lines 213-217 largely are not results, but sample site information.  Further, some of the statements lack literature citations.

These can be removed to section 2.1 of materials and methods where the sampling locations are introduced, and literature citations will be added as necessary.

• Line 265: remove comma after “column”. Line 330: phylum should be capitalized in both instances. Sentence on Line 355 is irrelevant to TEM results (section topic).  

Ok, we can make these changes.

• Passage on line 390-391 discusses predicted reductions in non-spinose foraminifera yet the reader has not been informed if N. pachyderma is spinose or non-spinose. 

We will make sure this is noted in the introduction – thank you for spotting this.

• The references for this statement are in line 402, as well as this being a personal observation.

The references for this statement are in line 402, as well as this being a personal observation.

• Line 416: What is a detrital diatom? 

Diatoms that are dead and part of the detritus. This can be made clearer.

• Why are bacteria necessarily linked to the diatoms (lines ~415-418)?  Bacteria and archaea can live independently from diatoms.

Yes, we agree that bacteria and archaea can live independently from diatoms. This sentence relates to the discussion at lines 472-481 on the bacteria, and in particular the flavobacteria found in the diatom phycosphere, and their greater relative abundance in the foram than in the water column. This is hypothesised to be a function of the large numbers of flavobacteria feeding in the phycosphere, so as N. pachyderma eats the diatom, it also consumes these bacteria disproportionally to other species not associated with the phycosphere. It does not exclude the idea that bacteria could also be taken up directly from the water column and from other kinds of POM. We can add a clarifying statement here.

• Line 425-426 notes twice that there are eight core ASVs in microbiome yet Table 2 lists nine “core” ASVs in microbiome (see also line 433).  Why the difference?  Which is correct?  

There are nine core ASVs. Thank you for highlighting this error. They should read eight of nine and seven of nine respectively and will be corrected.

• It is not clear how some specimens were denoted “potentially gametogenic” (lines 462, 525-526).  No data is presented on this (not in tables, etc). 

The possibility of gametogenic specimens is raised in line 425 where the limited numbers of ASVs in 2 specimens is highlighted. Forams which are about to produce gametes are known to stop feeding, and this is a potential explanation for the reduced numbers of ASVs identified in the two specimens. Hence the term “potentially gametogenic” at lines 462 and 525-526. We can add a brief reminder at each of these lines as to why the foram in question is defined as “potentially gametogenic”. Of course, there may be other explanations, such as natural variation, potentially dying specimens (perhaps due to a virus), that we could also highlight.

• Discussion of light use by foraminifera appears on lines 487 to 488 yet light levels are not reported in the data presented here. 

Light use is not discussed in relation to the foraminifer, but in relation to ASV74 which is assigned to the order Cellvibrionales many of which can utilise light in bacterial photosynthesis/energy generation. Since our N. pachyderma samples were collected from the photic zone (above 200m), it is likely that some of the bacteria they ingest are photosynthetic. ASV47 is a core member of the microbiome and therefore was discussed in that context, as likely to be photosynthetic, or using rhodopsin for energy generation.

• Line 493 is oddly worded—how can microbes be clustered in a gene? 

This should read “nifH sequences that cluster with Bradyrhizobium nifH sequences” and will be corrected.

• The passage from Line ~493 to 497 is confusing because it seems to be advocating that these foram populations are N₂-fixing but that was not measured.  Further, it is not clear that “our findings” on line 497 are supported by Fernandez-Mendez et al. (2016). 

This is a discussion on the metabolism of the bacteria that are taxonomically assigned to particular ASVs, and not on the metabolism of the foraminifera. ASV116 is assigned to the nitrogen fixing Bradyrhizobium, and it is a core microbiome constituent. We highlight here, that our data on the presence of these organisms agrees with previous data showing their abundance in the region compared to other nifH types. We clearly have not communicated this well enough and will clarify.

• Authors must explain why ASV27 is called Aurantivirga (line 498 and perhaps elsewhere) yet lines 503 to 505 says it is a Tenacibaculum species.  Which is the reader to believe? Then the authors pontificate about fish teeth and how this ASV27 provides extra calcium to the foraminifer for calcification, which is pure speculation. 

Aurantivirgia and Tenacibaculum are members of the Flavobacteriaceae. ASV27 was identified as Aurantivirgia in the SILVA database taxonomic assignment, and we discuss the basic characteristics of Aurantivirgia in lines 502-503. We also carried out a BLASTn search of the NCBI database on this ASV and the highest match was Tenacibaculum. Therefore, in relation to ASV27 we also discuss this genus.

The reviewer has misunderstood the role of Tenacibaculum here. They do not provide calcium, but utilise it to promote their growth, this is why they are found associated with fish teeth, and why the foraminiferal test would be an attractive niche for this bacterium. We will work to shorten and clarify this.

• Line 537: please explain what “intracellular ingestion” is.  Ingestion is the act of taking something from outside the cell / body into the cell / body.  Most biologists would simply say the foram phagocytoses the complete diatom (frustule + cell). 

We can reword this. We are trying to highlight that N. pachyderma phagocytoses the complete diatom, and then digests the cell (but arguably not the chloroplast straight away) as opposed to many benthic foraminifera which crack open the frustule externally and phagocytose the soft cell material leaving the frustule on the outside. The term “intracellular ingestion” was used by Pinko et al 2023 to describe this, (cited in the manuscript) but we are happy to reword it.

• While the term kleptoplasty was used three times in the Abstract and once earlier in the contribution (line 440), it is not until section 4.4 that “kleptoplastic behaviour” is asserted for N. pachyderma. The term is never fully defined although a partial definition appears on line ~544. 

Again, we wish to make clear that we are not asserting the N. pachyderma is kleptoplastic. But the reviewer makes an excellent point that we have not defined it. Given that there may be other roles for kleptoplasts other than the traditional photosynthetic role, we will fully define and explain this.

• Provide references for foraminifera, ciliates and dinoflagellates that are kleptoplastic (line 543).   

This will be done.

• Proper spelling is “byproduct” line 549, vs “biproduct”.

Apologies. This will be corrected.

• The citation of LeKieffre et al. (2018) on line 554 should be the LeKieffre et al. 2018 paper in Marine Micropaleontolgy, not the one in Mar. Biol.  The citation on line 583 is properly cited as the 2018 Mar. Biol. paper.

This will be inserted as 2018a and the marine biology citation as 2018b in accordance with alphabetical names.

• Powers et al. (2022, Frontiers in Mar. Sci.) should be cited on line 575, with Gomaa et al., as these two papers describe some of the functions of the N. stella kleptoplasts via gene expression (transcriptomics). 

Ok.

• Regarding mixotrophy and kleptoplasty in foraminifera (line 583), I believe Cedhagen (1991) documented this long ago for Nonionellina labradorica. That paper should be cited somewhere in paragraph spanning lines 598 to 604.  

Whilst we have cited this paper earlier, we will also include it here.

• Authors are reminded that many (perhaps most) forams do not have carbonate tests (shells), so that should be noted in passage about geochemistry (~ line 625). 

This is very true, and we are grateful for the reminder, and will add this.

• What exactly is “metabolic C” (line 628)?  An internet search reveals it is a type of health supplement of Vitamin C.

Our apologies that this is indeed unclear. C is carbon. In this context the metabolic carbon is that which has been produced in respiration inside the cell (by endobionts) and so has an offset C-isotopic ratio that can be reflected in the shell C isotopic ratios. We can add an explanatory sentence here.

• Line 630: The phrase “sediment assemblage” typically refers to the benthos (organisms that live on or in the seafloor). Perhaps authors intend “fossil record” or “sedimentological record” instead? 

Yes, we do. Thank you for the correction.

• Line 633 to 634 should add “calcareous” to read “…throughout the lifetime of calcareous foraminifera (Spindler…”. 

Ok

• Statement on line 641 should change as photosynthesis was not shown, only inferred. 

We see that the reviewer has misunderstood what we are attempting to communicate, so we will reword these sentences. Here, again, we are not trying to suggest that photosynthesis has been proven or is happening, but that since photosynthesis is known to influence calcareous shell isotopic chemistry, there is an urgent need to determine if it is occurring (and its seasonality, facultative/obligate nature etc) so that we can apply this biological understanding to interpretation of the geochemistry and palaeorecord.

• Line 731 should be italicized (see same genus on prior page).

Thanks for spotting this.

Mechanics (also important):

• The tense of the document is a mix of past and present, often in the same sentence; most scientific papers are in past tense.  Please change lines 17 to “used”, line 19 to “was”, line 20 “consisted of”, lines 217 - 219 should be past tense, etc.

We will check through all the document to gain consistency in past tense.

• Readers who are red-green color blind will be significantly challenged while reading Figures 3, 4, 5, A1, A2, A3, and A4.  The authors should consider changing their color palettes, datum point shapes, etc. 

The colours have been specifically chosen using the Coblis-Colour blindness Simulator as recommended in the submission portal. According to this simulator the chosen colours are suitable for a range of colour vision deficiencies including red-green.

• More reference strings should begin with “e.g.,” because the cited papers are only examples and not an exhaustive list:  lines 52, 440, 557, 634.  For line 557-558, it is surprising that Bernhard and Bowser 1999 Earth Sci. Reviews is not cited as it compiled all known foraminifera kleptoplasty cases to that time. 

Ok, we will add e.g., and we agree that Bernhard and Bowser should certainly be cited and will add this.

• Remove colloquial wording (e.g., line 49 “…will find itself spatially… should be “will be spatially…”; line 171: “…was carried out…” should be “…was executed…” or similar; lines 272-273 “a degree of clustering” should read “shows clustering…”; line 305 “six out of the seven” should be “six of seven”; line 464: “break down” should read “degrade”; line 466: “carry out” should read “ perform”.  Line 669 to 670 is obtuse (“There is a degree of clustering…”).
• Lines 115, 772: Ship names are always italicized.
• For Figure 1: suggest using different color or shape for symbols in the two different sampling years.  Resolution will be, presumably, better than that provided for review. 

We will address all these points.

• Methods seem a bit too detailed (e.g., passage from lines 143-148). 

We are happy to go through the methods and make them more concise. However, in the example given here, the PCR amplifications were rather different from protocols used elsewhere, perhaps a reflection on PCR requirements for forams stored in RNALater, and since this protocol is not available elsewhere, we have included it.

• Please fix font style and size (“t” in “taxa” on, e.g., lines 279, 329; 521).  
• Line 473 “sp.” should not be italicized, ever. 
• Suggest authors comb the text for errors in punctuation, etc. For example, see lines 512, 551, 561 (remove comma before parenthetic). 
• The order of the key in Figs. A1 and A2 is peculiar because it goes from 0 to 100, to 150 to 200 to 50.  Most would arrange from 0 to 50 to 100 to 150 to 200.  The gray background in those figures is inappropriate (waste of ink / electrons).

We will address all these points.

• The Conclusions section is blank / non-existent.

Our sincere apologies for this. It will be rectified.

• References were not proofread by authors.  Issues are (a) at least 46 species names have not been italicized; (b) at least six entries lack the journal name; (c) some entries are gibberish (e.g., Bell & Mitchell, Brummer et al – see penultimate author name); (d) lack of URL for software packages (Lahti); (e) lack of publisher in at least 2 references (Eegeesiak et al., Schiebel and Hemleben); (f) font color is inconsistent; (g) missing spaces between words, (h) inconsistent presentation of journals (some names abbreviated, others not), (i) lack of superscripting isotopes, (j) inconsistent line spacing. 

Our apologies for this. We did proofread our document but acknowledge that there are regrettably several small errors. The authors used a new citation tool for this manuscript and clearly had some teething trouble. We will amend and double check all references.