This is a rich study that explores how oxygen depletion shapes carbon, nitrogen, and phosphorus cycling in the northern Benguela Upwelling System (NBUS). What stands out most is the way the authors weave together multiple strands of evidence, from sediment chemistry to porewater gradients, incubation fluxes, and water-column data to build a cohesive picture of benthic–pelagic interactions across a redox gradient. It’s a relevant contribution, especially given the growing interest in how ocean deoxygenation might reshape nutrient stoichiometry and microbial dynamics in coastal and upwelling systems. One of the strengths of this paper lies in how it brings to light less commonly discussed phosphorus pools, like those tied to fish debris and sulphur-oxidizing bacteria — and connects them to shifts in N:P ratios that challenge some classical Redfield-based thinking.

That said, I’d encourage a bit more caution in how some findings are framed. The N deficit is widely used as a shorthand for identifying deviations from Redfield ratios, but it’s not necessarily meant to trace mechanistic pathways like denitrification or anammox without further support. The data here don’t invalidate the metric, but they offer a reminder that benthic P inputs can skew its interpretation. Reframing this not as a correction of the metric, but as a call for more nuanced use under certain benthic conditions, would make the authors message more balanced to a broader readership.

I also think the paper would benefit from more explicit acknowledgment of temporal variability. While the authors do a good job highlighting spatial differences across the shelf and slope, it’s worth underscoring that processes like P release, redox fluctuations, or fish debris deposition can vary a lot seasonally or even episodically. Since the dataset comes from a single cruise, it’s important not to overgeneralize to long-term OMZ dynamics.A brief acknowledgement of this limitation, coupled with suggestions for future time-series studies, would guard against over-generalisation.

Given the extreme, near-permanent hypoxia/euxinia on the Namibian shelf, not deeply addressing bioturbation is reasonable. On the upper slope, some residual fauna and irrigation likely occur; the paper could have acknowledged that. So while bioturbation isn’t underestimated in the sense of missing a major driver, a statement such as “macro-faunal bioturbation is assumed negligible on the hypoxic shelf and minimal on the upper slope …” could close that narrative gap.

A concern is the apparent mismatch between diffusive flux estimates calculated with Fick’s law and the considerably larger whole-core incubation fluxes, especially for DIC, which at two sites exceed one mole per square meter per day. Do authors think that it raises the possibility of incubation artefacts (e.g. over-stirring, boundary-layer collapse) or uncertainties in porosity? Perhaps providing core geometry, stirring rates, and an uncertainty analysis (for example, how a ±10 % error in porosity or gradient might shift the calculated fluxes) would bolster confidence in the flux comparison.

The causal link between SOB activity and enhanced P release supports much of the paper’s narrative, yet the evidence remains inferential. The authors should note explicitly that the SOB mechanism remains a hypothesis to be tested with future cell counts, FISH, metagenomics or poly-P assays.

Overall, I think this is a strong and well-argued paper. My suggestions are meant to sharpen some of the framing. I’ve included below a list of more specific and technical comments that I hope will be useful as the authors move toward a final revision.

Introduction

Line 25: I suggest authors to specify which chemical analysis in “Chemical analysis indicates that a large proportion of the highly reactive sedimentary P pool consists of (i) P supplied in fish debris rather than marine algal biomass and/or (ii) P accumulated intracellularly by sulphide-oxidizing bacteria (SOB).”, to make the statement more robust and with stronger geochemical constraints.

Line 39: I recommend authors to change “...oxygen depletion boosts anaerobic N transformation processes in the water column and sediment that represent a net sink for N…” to “…oxygen depletion enhances anaerobic nitrogen transformation processes in the water column and sediments, which represent a net sink for nitrogen…”. The change of “that” to “which”  works better for a non-restrictive clause.

Line 53: I suggest authors to change “relevant to study” to “"relevant for studying" or "suitable for study"

Line 87: add the date to Kuster-Heins et al.

Line 105: substitute “The” by “the”

Line 108: the sentence with “productivity” and “and oxygen depletion” is separated by Figure 1 caption.

Line 128: I suggest authors to substitute “holding with” by “equipped with”

Line 130: I suggest substituting: "Immediately after the CTD/rosette with sampling bottles was back on deck..." to "Immediately after recovery of the CTD rosette..."

Line 132 and 143: I suggest substituting “filtered over a 0.8/0.2 µm syringe filter” with “"filtered through a 0.8/0.2 µm Pall Acropak syringe”

Line 133: I suggest substituting “After sampling all bottles..." by “"Once all bottles had been sampled..."

Line 137: The sentence “Samples for HPO4 2- and Si were acidified to pH ~1” seems a bit vague. I suggest authors to changed to something like "Samples for HPO₄²⁻ and Si analysis were acidified to ~pH 1 before storage."

Line 145: The phrasing “digestion of (particulate) organic compound” could be improved to something as “"preceded by digestion of particulate organic matter"

Chapter 2.2: I am missing references to procedural blanks, analytical replicates performed and/or certified reference materials (CRMs) analysis. Could flux calculations propagate ±10 % in pore-water gradients and flip flux direction for NO₃⁻ at low concentrations?

Line 151: I suggest authors to substitute “were otherwise undisturbed” to ““and showed no visible signs of disturbance”

Line 154: I recommend authors to substitute “Profiles were aborted when O₂ reached 0.” To “Profiling was stopped once O₂ concentrations approached zero.”, to avoid colloquial language.

Line 167: “sea salt from seawater” reads redundant. I recommend authors change it to “sea salt content” or other.

Line 247: You write that OMZ stations are “better oxygenated (65 µmol L⁻¹)” than shelf stations (3–10 µmol L⁻¹), which is accurate  but might confuse readers, since OMZ is normally low-O₂ by definition. I suggest clarify that the OMZ here refers to intermediate depths within the perennial OMZ, but bottom waters were more oxygenated than on the shallow shelf.

Line 249: I suggest authors to better precise the sentence “that were the lowest of the investigated transect”, perhaps changing it to “surface sediment with the lowest TOC contents”

Line 250: add “the” before “lowest”

Line 263: I recommend authors to substitute “(much)” to “considerably” or “significantly”, if statistically based.

Line 278: There is a mismatching parenthesis here.

Line 280: “Fetot/Stot » should be consistent with the previous notation.

Line 281: “PR-Fe” (poorly reactive Fe) is used appropriately but without defining it clearly until later. Perhaps include a brief clarification upfront, e.g., “...dominated by poorly reactive (PR-Fe; e.g., silicate-bound or crystalline) iron...”

Libe 335: “We first note that DOP calculated as total dissolved P minus P…” This sentence equals to: ““...calculated as the difference between total dissolved P and HPO₄²⁻”?

Line 336: You rightly flag that DOP often results in negative values. Could there be error sources such as analytical uncertainty in total dissolved P, precipitation or adsorption of HPO₄²⁻ during sampling or the presence of colloidal P not fully removed by filtration? Maybe briefly acknowledge these limitations to reinforce confidence in your interpretation.

Line 354: by “scaled” you mean “correlated “?

Line 436: There is a grammatical error after “10 cm of” (incomplete phrase).

Line 464: Here, the logical connections between observation and interpretations are implied but not explicitly stated. I suggest authors change “In an alternative process of sink switching, this additional accumulation of pore-water HPO₄²⁻ then drives authigenic precipitation…” for “This accumulation of pore-water HPO₄²⁻ may instead promote authigenic precipitation…”

Line 478> You acknowledge heterogeneity in P content due to patchy fish debris, which raises an important issue: the spatial variability in fish bone deposition is poorly constrained and a source of bias in P budgets. Could be interesting to mention that sediment imaging, bone counts or other techniches which might help constrain this in the future.

Line 479: Here it should be “heterogeneous”, as well as in line 620.

Line 503: If exploratory data (NMR or genetic results) are used to support an interpretation, I suggest they are shown.

Line 528: I suggest authors review the text for opportunities to remove redundant modifiers such as "relatively high," "very low," "generally small" where precise values are already provided.

Line 532: remove the repeated "st"

Line 584: However, it would help the reader if the authors could briefly clarify how they distinguish this signal from alternative processes such as nitrate diffusion from overlying water or residual nitrate from incomplete denitrification. Even a short sentence acknowledging these possibilities.

Line 704: The authors write that “This calls into question how accurate the term ‘N deficit’ is in the NBUS and perhaps more broadly in upwelling regions…” While this is provocative and potentially important, maybe it lacks sufficient framing. The N deficit is commonly defined as a diagnostic proxy, not a mechanistic metric. It reflects deviations from Redfield stoichiometry but does not inherently imply anaerobic N loss unless this is clearly demonstrated through isotopic, process-rate, or mass balance data. I recommend you clearly distinguish between "apparent N deficit" (i.e., deviation from expected N:P) and the mechanistic N loss processes (denitrification, anammox) often inferred from it. Avoid suggesting the metric is "inaccurate"; rather, emphasize that its interpretation requires careful evaluation of benthic P sources.

Linbe 678: Authors assume that 2 umol/L would have been the concentration of HPO42- in bottom waters at stations 5, 6 and 10 as well in the hypothetical absence of the sediment-derived bottom-water HPO4 2- enrichment. I suggest them to better justify this  or acknowledge more explicitly that the value is a conservative estimate to illustrate potential P-driven contribution to the N deficit, not a precise background level.