Overall, the manuscript has some value because of the value of the data provided (not very common to see this number of dark dic fixation measurements in relation to primary production rates). However, the writing is a bit sloppy, and the novelty of the study is not as high as suggested by the authors. This is because, currently, this manuscript is critically missing some very relevant citations, which need to be included,  so that the readers get a more accurate understanding of the novelty of this manuscript (see specific comments below). Also, several of the main claims are not supported by data of this manuscript (see also specific comments below).

l.36-48- one key citation, that exactly looked on the contribution of DIC fixation to bacterial carbon demand is missing is this work, and should be included throughout this manuscript (Baltar, …Herndl, et al., 2010 GRL, doi:10.1029/2010GL043105: “Significance of non‐sinking particulate organic carbon and dark CO2 fixation to heterotrophic carbon demand in the mesopelagic northeast Atlantic”. This shows that the idea of looking into the contribution of dic fixation to MCD is not novel from the current manuscript, but has been explored before.

- Related to this point, another key citation that is surprisingly not included in this manuscript, is Baltar & Herndl, Biogeosciences 2019 (https://doi.org/10.5194/bg-16-3793-2019): “Ideas and perspectives: Is dark carbon fixation relevant for oceanic primary production estimates?”.  This paper did actually raise awareness about the relevance of DIC fixation and quantified how it compares to primary production estimates in the ocean. Thus, to be fair with previous research, and fair and accurate to the readers, the findings of the current manuscript should take into consideration what others have found before. For example, when looking into the main findings of this manuscript, mentioned in the last paragprah of the Introduction: this point in l.72-73 (“Our results demonstrate that DCF rates cannot be negleted (contrary to past conventions, Nielsen 1952))” was already concluded/mentioned in the Baltar & Herndl 2019 paper. In l. 74- 75. The other outcome (“We also show that DCF substantially contributes to bacterial carbon demand (BCD)”) was also already shown by Baltar etc a 2010 GRL (although in the current paper is focused on the Med Sea, and in the case of Baltar et al 2010 it was focused on the Atlantic; but still, this information cannot be neglected).

L. 99. specify what type/material of bottles. This is relevant for light productivity.

- what was the temperature of the incubation? relative to in situ conditions. This is very important due to the strong shift in temperature from 0 to >1500 meters.

L.119. What 100 nM was used? seems quite high for an oligotrophic site.

- the number of replicates and blanks is currently missing; needs to be included.

- The methods are missing a detailed description of how the BCD were calculated (and the contribution of DCF to BCD). This is particularly relevant because respiration was not directly estimated in this study, but it was indirectly derived.

- To properly distinguished the “mixed” and “staritifed” periods, the authors could also include the Temperature and Salinity (and/or density) plots, to show the level of stratification, and support their period clasification.

Table 1. Not clear if those numbers are an interval of confidence or a range. This should be specified in the caption. And also, a measure of variability (SD, or  SE,..) should be included.

Also, the limitations of the assumptions in this ms (ie, “Assuming bacterial gross efficiency of 0.2 (Gasol et al., 1998) and that the available DOC for bacteria is 20% of the total primary productivity at the photic layer (Teira et al., 2003)”  should be discussed in the discussion of this manuscript.

- l. 207. Before it was mentioned they used the BGW by Gasol 1998, and here that they use the one from Doval 2001….this needs to be consistent.

-l. 212-215. All this is based on the contribution from DOC; but what about the contribution of POC?

-l. 230-233. Here is mentioned that the nutrients “in the deep aphotic water were similar overall between periods (not shown)”; but in the methods section it was mentioned that nutrients were measured only in 2 of the 6 stations. Thus, it seems to me that this data is ‘not show’ because is not available, and therefore this statement cannot be sustained.

-l 239-241. “therefore we surmise they have a preferential particle-attached”. There is no data in this study to support this claim

l.246. The microbial carbon pump citation is Jiao et al 2010, but not Herndl and Reinthaler 2013.

l. 250-257. The authors mention that the negative correlation they find between ammonia and nitrite to DCF is indicative of an important metabolic pathway yielding energy for fix DIC in the aphotic zone. However, this does not make too much sense to me. The relation, for example, between ammonium oxidisers and DIC fixation should be positive and not negative, to support the relation of ammonium as an energy source of DIC fixation (see Agogue, ..Herndl et al., 2008, Nature). In fact, the same authors seem to agree with what I mention when they write right afterwards:  “In agreement, both ammonia and nitrite oxidizers were found in the aphotic zone of all cruises (discussion below), further highlighting their potential role as contributors to DCF in southeast Mediterranean Sea”… meaning a positive relation (presence of both things: nutrients and DCF fix rates) would indicate that one relies on the other…In fact, this negative relation is probably more an indirect effect of the normal changes observed with depth in nutrient concentration in the water column. Thus, the argument in this paragraph is not supported by the data.

l. 265-276. The authors mention “Analyses of 16S rRNA gene amplicons suggest that diverse bacteria and archaea may drive DCF in the aphotic southeast Mediterranean Sea (Fig 4A)”. However, the 16S analysis can only provide a general community composition and diversity of the overall community, but it does not provide a direct link between these individuales and the DCF. In other words, it cannot indicate which of all the members of the community is performing DCF. This, their argument is also not supported by the data they provide.

l. 281. I believe the citation Baltar et al 2022 might be outdated. This was a preprint but I think they published the final version of the paper in Nature Microbiology in 2023 or 2024. This should be updated.

l.300-302. Based on all the assumptions and limitations of the present study I would not sue the expression “it is clear that” in this sentence.

Overall the Conclusion paragraph seems quite weak. imprecise and unstructured. Also on of the final statements  (“Our study highlights the need for adding DCF measurements to global carbon budgets”), was already mentioned by the Baltar,..,Herndl et al 2010, GRL, article. So, it should be also mentioned in here.

The manuscript by Reich et al., “Dark inorganic carbon fixation contributes to bacterial organic carbon demand in the oligotrophic Southeastern Mediterranean Sea” presents novel measurements of light and dark primary productivity as well as bacterial productivity across the whole water column at 6 time points. The authors conclude that dark carbon fixation by chemoauthotrophy is a quantitatively relevant process that can account for a substantial portion, on some occasions even fully, of the bacterial carbon demand in aphotic layers of the water column. The authors address an important topic and provide a novel, comprehensive dataset on productivity rates. I therefore recommend the manuscript for publication, after the following comments have been addressed:

• Discussion: While the discussion touches on the most relevant points, it is in part missing depth and structure. I recommend restructuring it by using subheadings. Several questions remain open, e.g., what is the reason for the spatial variation of DCF across the water column (Fig. 3)? What could be limiting factors for each of the rates presented, that would explain their spatiotemporal pattern? A systematic discussion of these factors together with their uncertainties would substantiate the discussion.
• Conclusion: One of the conclusions is that the dark carbon fixation can not always cover the full bacterial carbon demand, requiring to assess additional carbon sources. I would recommend to add a description on uncertainties here, by systematically assessing the calculation of bacterial carbon demand and the parameters and assumptions (e.g. growth efficiencies, percentage of DOC exudation of primary productivity (see Thornton et al., 2014), …) that feed into it. Such a detailed uncertainty assessment would build more confidence in the final conclusion.
• Carbon budget in Fig. 5: does the budget consider that LPP only occurs during daylight periods, whereas DCF does not follow such constraints? Where does the DOC from bacterial production originally comes from (I would assume there is rather bacterial uptake, or am I missing sth)?
• Methods: Samples were incubated under “ambient light conditions” (l. 101) or under “ambient temperatures” (l. 121), but it is never specified what these conditions are. A table including all sample depth, the respective light and temperature condition, together with the final data is required for a comprehensive description. Please also comment on the fact that they were not incubated under in-situ pressure, especially in light of recent publications (Amano et al., 2022).
• Lateral transport: The profiles were discussed mainly in the context of in-situ data. However, they are taken in a fluid and dynamic environment. A short paragraph discussing lateral aspects as a driver of variability would help to set the results in context. For example, what is the main flow direction of the water at the location of the profile? How variable are physicochemical parameters in the horizontal direction (e.g. from satellite data?)?

Minor comments:

• 37: remove “pool”
• 39: throughout the manuscript, there are some occasions of vague formulations, e.g. “exported through photosynthesis”. Please doublecheck for vague formulations throughout the manuscript.
• 162, “than” instead of “then”
• 168: Results of BCD are presented here, but it is not described in the methods how this was calculated. I recommend to briefly provide the equation in the methods section.
• 181-186: This sentence is hard to read, consider splitting it into several parts.
• 207: “literature” instead of “literary”
• 212-213: a word is missing in this sentence, making it difficult to understand
• 330-333: the sentence about “operational opportunities” comes a bit out of the blue here and is not connected to the original scope of the study, I recommend deleting it.
• 312: “DOC exudation from LPP was 20% of the rates.”, for clarity, better to write “DOC exudation from LPP was assumed to be 20% of the rates.”, since this was not measured.

References

Thornton, D. C. (2014). Dissolved organic matter (DOM) release by phytoplankton in the contemporary and future ocean. European Journal of Phycology, 49(1), 20-46.

Amano, C., Zhao, Z., Sintes, E., Reinthaler, T., Stefanschitz, J., Kisadur, M., ... & Herndl, G. J. (2022). Limited carbon cycling due to high-pressure effects on the deep-sea microbiome. Nature Geoscience, 15(12), 1041-1047.