Please see my full comments in the attached pdf. 

Limited physical protection leads to high organic carbon reactivity in anoxic Baltic Sea sediments

General Assessment:

This manuscript addresses a timely and relevant topic in sedimentary organic carbon dynamics under varying redox conditions. While the subject is of clear interest to the biogeoscience community, I find that the study, in its current form, falls short in several key areas that significantly limit its impact and interpretive strength.

Most critically, the data presented are sparse and inconsistently applied across stations, with core analytical components (e.g., δ¹³C, Fe-bound OC) performed only at select sites, and important parameters such as Δ¹⁴C not included at all. This uneven dataset complicates cross-site comparisons and weakens the manuscript's overarching conclusions. Several of the interpretations appear speculative and are not strongly supported by the data. Furthermore, the discussion lacks depth in many areas, especially regarding key observations in the POC and SRR profiles, and the potential mineralogical and microbial controls on OC preservation (expanded below in “comments”).

The manuscript would benefit from a more robust theoretical framework and a clearer connection between the presented data and the cited literature. Some central concepts—such as mineral phase protection, particle shuttling, and OC-Fe associations—are mentioned but not fully developed or critically examined in light of the actual data.

Comments:

Line 37: "... role in regulating the sediment biogeochemistry and faunal community, which in turn influence OC cycling??" As currently written, the linkage to OC remineralization is vague and needs to be explicitly connected to the broader context introduced in the preceding sentence.

Lines 39-43: These paragraphs read awkwardly.  The authors initially suggest that anoxia promotes OC preservation but then shift to discussing the role of oxygen in anabolism. Although these concepts are related, the logic and flow need clarification.

 Also, the sentence about complex molecules being more easily degraded via aerobic pathways lacks detail. What specific compounds are meant here?

The statement regarding certain compounds requiring oxygen for degradation would benefit from examples and context. How representative are these compounds relative to bulk OC? And the distinction between points (ii) and (iii) is unclear and may be redundant. Please re-word this.

Line 43: What about discussing the role of microbial consortia in OC remineralization? This will strengthen your arguments

Lines 110-112: Please provide more details on the standards used for stable carbon isotope analyses, as well as QA/QC measures. Information on how linearity, drift, and reproducibility were assessed would strengthen the methodological section.

Line 113: Table SI 1 not displaying this, but Lalonde method.

Line 123: Was there a rationale for using plastic Falcon tubes for OC analysis? These are generally not recommended due to potential contamination. Why were pre-combusted glass vials not used?

Lines 127-128: More information is needed regarding cleaning protocols for filters and collection containers.

Lines 155-157: You acknowledge that ²¹⁰Pb-derived OC age estimates do not capture all relevant degradation pathways, yet no further discussion is provided. Consider elaborating on how this methodological limitation may influence your conclusions, and whether complementary proxies were considered.

Lines 160-165: The statement that POC profiles are "similar" across sites oversimplifies the data. For example:

* WGB1 has lower surface concentrations and a more gradual decline with depth than WGB2 and WGB3.

*WGB4 shows an apparent increase below 5 cm.

These contrasting profiles merit discussion. Avoid generalizations that obscure site-specific differences.

Line 165: Only δ¹³C data from WGB1 and WGB2 are shown, yet the sentence discusses WGB2 and WGB3. Consider presenting δ¹³C data from all stations for consistency and interpretive strength.

Lines 164-169: Vague statement.

Lines 170-173: As mentioned for POC, the discussion regarding SRR is brief and does not adequately address key variations between stations.

For example: there are striking differences in SRR between WGB2 and 3, the latter displaying much higher values, sharply decreasing with depth in the top 5 cm, while the WGB2 has a relatively uniform SRR. How does this and the fact that their POC profiles are similar do not grant any further discussion?

Similar remarks can be made for WGB4 and WGB5,  which display similar SRR but contrasting POC depth patterns.  These observations deserve further discussion beyond a simple correlation with OC reactivity.

Line 174: The term “OC age” is potentially misleading, especially in the absence of radiocarbon data. This may lead to misinterpretation of your findings.

Line 182: Please use terminology consistently. “OC age” is not appropriate for ²¹⁰Pb-based estimates. The figure refers to “sediment age,” which should be used throughout for clarity.

Lines 186: The explanation and analysis of this is quite superficial, there is little exploration of why some station plot toward one line and others to the anoxic line. Some samples are split in between. Without independent proxies of OC reactivity, the conclusion lacks sufficient support.

Lines 185-190: This paragraph is somewhat tangential. The connection to the Vatsev study is not clearly explained, and the comment on zooplankton targeting reactive OC appears speculative. Consider focusing more directly on how your results relate to established degradation mechanisms.

Lines 190-192: The cited literature primarily addresses mineral associations with terrestrial OC, which differs from your dataset dominated by marine-derived material. The relevance of these studies to your interpretations should be clarified.

Lines 194-195: It would be important to contrast the lability of marine-derived OC from phytoplankton blooms with terrestrial OM. Much of the literature on mineral phase protection involves terrestrial inputs, which are not considered here.

Line 225: Figures 3 and 4 refer to “data per station,” but it is unclear which depths or samples are included. Are all depths shown? Why are there more data points in Figure 3 than Figure 4, despite nearly identical captions? ("data are represented per station...").

Also, consider incorporating sediment depth into the figure using a color bar or symbol shading to help convey vertical structure in the data.

Line 228: I cannot see this in the supplement available, also, why are not you showing all the depth in Figure 4? Which depth and which rationale was used to show some of the data there.

Line 230-240: The entire section here reads as a summary of disconnected concepts rather than a coherent interpretation.  It’s unclear which data is plotted in Figure 4; are all depths included? (most likely not given the # of dots).

There's no discussion of how OC/SSA relates to SRR or OC%. We cannot assess why some surficial (circled) samples behave so different in the POC / SSA space, with WGB3 and 1 plotting below the OC/SSA= 10 line.

This section would benefit from a more detailed analysis of the relationship between OC loading and measured SRR values. Currently, key patterns in the SRR data are not addressed, and their relevance to the OC/SSA trends remains unclear. For example, the surface sample at WGB3 exhibits the highest SRR among all stations, with a sharp decline downcore, whereas WGB1 shows much lower SRR values, yet it plots closer to the OC/SSA = 1 line. Similarly, WGB4 and WGB5 exhibit a marked decrease in OC loading with depth, while WGB2 displays a more subtle pattern despite having a comparable SRR profile. These contrasts suggest decoupling between OC reactivity and mineral association that deserve further exploration. A more integrated discussion connecting SRR profiles with OC/SSA trends is needed to support the interpretations in this section.

Lines 244-280: The entire section 3.3 is highly speculative. It brings up numerous concepts from literature without clearly linking them with study data.

* How you could confidently assess the role of physical protection by only accounting for Fe-OC; there are other mineral phases well known to aid preservation of OC, besides Fe-OC.

* The analysis of Fe-bound OC is limited to only two stations and lacks interpretive depth.

* Is OC-Fe from WGB2 real, or an artifact of the extraction procedure? WGB2 appears to show erratic Fe-OC values (only 2 points have OC-Fe > 0) without clear depth trends, yet this is not discussed. In the manuscript only ranges are discussed, which indeed does not tell much.

* Nothing is mentioned regarding the fact that WGB1 has significantly lower FeR than the other profile. Why? What drives this behavior?

*How do authors explain the lack of OC-Fe at WGB 2 vs the 5% at WGB1, when the latter has much lower FeR ?

*If WGB2 is characterized as anoxic, while WGB1 is described as hypoxic, how do the authors explain the higher FeR concentrations at WGB2? This seems counterintuitive, given that more reducing conditions typically promote FeR dissolution.

*How do you reconcile the fact that higher OC concentrations were measured at WGB2, where there is virtually no OC-Fe, and SRR are ~ to those funds at WGB1, but remain constant and not decreasing with depth.

*More integration with δ¹³C data could clarify early diagenetic pathways but is not attempted.

*It is speculated that FeR reduction may be driven by H₂S production, yet it is unclear whether the presented data support this interpretation. If H₂S formation is linked to elevated sulfate reduction rates, one would expect FeR depletion to be most pronounced in the upper sediments where SRR is highest. However, FeR concentrations appear relatively constant in the top 8 cm, with more substantial declines observed only below 10 cm. This pattern raises important questions: Why does FeR persist where SRR is elevated? What mechanisms might explain the delayed reduction of FeR at depth? Furthermore, how do the differing SRR profiles across stations reconcile with the FeR depth trends shown in Figure 5? These discrepancies deserve more thorough discussion to support the proposed mechanisms.

Lines 252-254: The reference to the black carbon sink is highly speculative, and it is unrelated to the data presented.

Lines 255-260: Statements about grain-size variation and mineralogical effects are vague. Please be more specific about what these factors are and how they were evaluated in this study.

Lines 267-268 The phrase “shuttling of particles toward deeper parts of the basins” is unclear. What process is being referred to, and what evidence supports this interpretation?

Additional Comments:

Lines 23-24: Clarify what is meant by “large sources of OC.” Are you referring to marine organic matter, or another pool?

Line 30: Add reference for CO2/O2 regulation

Line 48: Consider specifying “bacterial mineralization” for clarity.

Line 95: Figure 1, invert the colorbar, so that 0 m is at the top and 450 m at the bottom.

Section 3.2 appears to be missing. The manuscript jumps from Section 3.1 to 3.3.

Supplementary Fig S1: When working with δ¹³C : C:N bi-plots, it is advisable to plot against N/C (not C:N).

Review of:

Limited physical protection leads to high organic carbon reactivity in anoxic Baltic Sea sediments

by Placitu et al. 2025

Recognition

First of all, I acknowledge the substantial effort undertaken by the authors in conducting this sedimentary biogeochemical study in the Baltic Sea. The collection of sediment cores from five stations across the Western Gotland Basin, combined with the extensive analytical work represents a significant investment. The authors try to tackle a complex and important question regarding the controls on organic carbon preservation in oxygen-depleted marine environments.

My goal in reviewing this manuscript is to improve my understanding of the study, identify potential gaps in the logical framework, and ultimately contribute to enhancing the quality and impact of this research.

General comment

This study aims to challenge the traditional paradigm that anoxia inherently promotes OC preservation by examining the role of physical protection mechanisms, specifically mineral surface availability and OC-iron associations, in controlling OC reactivity and burial efficiency. Their approach combines sediment geochemical profiling, sulfate reduction rate (SRR) measurements, and targeted analyses of mineral-organic associations at five stations. The key finding is that despite long-term anoxia, organic carbon remains highly reactive due to limited physical protection, as indicated by high OC loadings and low OC-Fe associations.

While the study’s scientific questions are well aligned with the scope of Biogeosciences, the manuscript in its current form tends toward superficial and speculative interpretation. It also lacks sufficient integration of the dataset across all sampled stations. Specifically, the authors do not justify the use of cores collected from other sites than WGB1 and 2. Furthermore, this limited sampling weakens the extrapolation of their results in the current format. A better integration of all results could improve this. The authors do not necessarily need to provide additional data beyond what is available but should explicitly acknowledge these limitations and critically discuss how the restricted spatial coverage could influence the confidence in, and the extrapolation of, their conclusions.

The manuscript is generally clear and well-written but would gain from refining the narrative to center more firmly on the core dataset and better explain the connection with cited literature. The latter would help reduce the impression of superficial and speculative discussion.

With these revisions, the study has strong potential to provide valuable understandings into OC diagenesis in sediments overlayed by anoxic waters.

I therefore recommend major revisions to improve the integration and the discussion of the results, but I consider that this manuscript merits publication in Biogeosciences once these issues are addressed.

Specific comment

L82: Please consider using “sedimentary organic carbon (SOC)” rather than POC or sedimentary POC

L91-92: Could you please provide more details about the sampling of the two subcores? Specifically, how and where were they collected?

There are many acronyms. I think that, for better readability, it would be preferable to redefine them in each section (Introduction, Methods, Results)

Figure1: Depth should be positive

Table1: Is WGB1 constantly hypoxic or does it oscillate between hypoxic and anoxic conditions?

L119: Do you have data from another site (WGB3 to 5) to check for potential environmental gradient?

L146: Why only sulfate reduction and not other anoxic process using nitrate or Fe and Mn-oxydes

L149-150: These sediments are not all anoxic (WGB1). Did any trace of biological activity was visible?

L164-165: Could you please explain your reasoning behind your interpretation of « fresh material »?

L176: Please add the unit

L174-185: From my understanding, you didn’t use the same formula as Katsev and Crowe (2015). Could that affect the location of your data point relative to the two regression lines (oxic/anoxic) derived from Katsev and Crowe (2015)?

Figure3 (and 4): “individual points represent different sediment depths…” Could you find a way to depict depth in this figure, perhaps using a colour scale?

L205: remove the ( “(albeit all …”

L207-208: While I agree with that, the water column is anoxic in your study. I’m curious to know how resuspension events could influence OC mineralization process in anoxic water.

Figure4: Are all the data points showed? There are fewer than in Figure 3. Why is that?

L229-231: Do you have an explanation for this high OC loading? eutrophication of the Baltic Sea, large extent of the anoxic water mass, … ?

L240-241: Why not the OC reactivity rather than OC loading, which could allow for intense mineralization? Or maybe, does the increase of OC loading at the sediment surface results from relatively “recent” eutrophication rather than OC mineralization?