Review report on egusphere-2024-3192

The manuscript focuses on organic matter degradation rates in the Amsterdam harbor estuary according to strong anthropogenic influence through dredging activities, using spatial monitoring data and diverse incubation processes. The research is very interesting and meaningful for carbon cycle and greenhouse gas emission from the sediment in such impacted area. The topic of this manuscript fits well with the journal's scope, and the data collected highlighted a strong sampling effort and figures are of good quality.

However, it is important to address some issues in the manuscript before acceptance for publishment, here are some specific comments:

Line 80-82: more details in which way shifting salinity affected CH4 are needed (even if discussed in discussion, see comment “line 675-677”).

Line 87: reference is missing.

Line 89-92: yes, but give examples of naturally and anthropogenically induced sediment disturbance.

Line 111: avoid terms like “our”. Here use “the”. To be corrected throughout the manuscript (e. g. “our study” replaced by “the present study”…).

Line 122-123: out of context here…

Line 138-139: representative of dredged sediment conditioned on land? Is this conditioning the major process for dredged sediment? Line 151 mentioned sediment relocated in the sea. More explanations are needed to justify the choice of these open-air incubations.

Line 139: “our”?

Line 151-152: The rates shown are per year?

Line 155-156: how many cores replicates for each location?

Line 242-243: Even evident for the author, precise the reason to have 20 cm of overlying water.

Line 285: Why 37 days incubation period were chosen?

Line 581: Short range of these different values is needed.

Line 606: no () for the reference. Dauwe et al. (2001)

Line 642: Zander et al. (2022)

Line 675-677: include the concept of SMTZ (sulfate-methane transition zone)

Line 681: “depending on”

Line 687: I don't know if the conclusion needs to be so precise about the results of the study…

Additional comments:  where are the dredging locations on Fig. 1? Dredging affects the upstream and downstream areas of the estuary in a similar way? Please give some details on this subject. What would be the consequences of such an imbalance, according to quantity of sediment dredged in each zone? What about the sediment relocated in the sea in terms of potential carbon mineralization processes? And finally CO2/CH4 effluxes toward the atmosphere?

"Perturbation increases source-dependent organic matter degradation rates in estuarine sediments" by Guangnan Wu et al. is a comprehensive and well-executed study investigating the chemical characteristics of sediment organic matter in Rotterdam harbour and the potential response of sediment carbon stocks to human disturbances (i.e. dredging). The study employs a range of techniques in the basic characterization of samples along a salinity transect (bulk sediment C/N, del13C, BIT index and pyrolysis-GCMS analysis of macromolecular organic matter) followed by a set of incubation experiments (both classical whole-core and homogenized sediment subaerial set-ups) to show how remineralization processes respond to disturbance. The data is of high quality and is generally processed and interpreted well, with a high degree of integration between the various lines of evidence. Overall, the outcome is convincing and should be published. However, I outline below one key issue related to the data processing that requires more careful consideration in the text, and several minor comments that should be addressed.

Key issue:

In processing the results of the whole-core incubations, ammonium fluxes are used to estimate the fraction of the DIC flux that is derived from organic matter remineralization (results shown in Fig. 5e). This calculation assumes Redfield stocihiometry for the degrading material, i.e. ammonium and DIC from remineralization are released in the ratio 106:16. This may be valid for the marine end-member site 115 but not necessarily for riverine end-member site 21A. Considering the bulk sediment C/N ratio data it is likely that site 21A releases more DIC per mole ammonium, even if the most reactive fraction of the sedimentary organic matter is relatively nitrogen rich. I suggest that this uncertainty is somehow included in the calculations, for example by presenting additional bars in Fig. 5e or a summary table. This issue is important because the quantification of remineralization-derived DIC production in the whole-core incubations is used later in the study when comparing with rates in the subaerial incubations, ie. assessing by how much dredging of sediment onto land would stimulate remineralization. 

Minor comments:

Line 81-82: No need to highlight CH4 specifically. The point is valid for the balance between any given set of remineralization pathways.

Line 84-87: Consider rewording the sentence ("estuaries" appears to be used in both a general and a specific way in the same sentence) and add the reference.

Line 88: Should be "penetration depth".

Line 99: Make sure to use brackets correctly.

Line 123: Should be "dredged sediment".

Line 137-139: Should be "bottle incubations"

Line 139: Should be "Our results show..." or "We show..."

Line 141: Should be "the properties of OM influence..."

Line 162: Use "end-members" or similar, rather than "realm"

Line 213: Remove "an"

Line 220-229: It would be useful for a reader trying to reproduce this method to know how the HF was disposed of during the protocol. Is it evaporated at some stage? This is a dangerous chemical and lab protocols need to be carefully designed.

Line 229: Clarify that "MOM" here refers to the residue of the previous steps.

Line 283: It is not clear what is meant by "60% water-filled volume". It is difficult to estimate the porosity of freeze-dried and homogenized sediment after re-wetting due to changes in grain size distribution during these processing steps.

Line 345: "Asterisk/stars" not "asteroids". Also unclear what the arrows in the plot indicate, should they be pointed in the opposite direction to link the numerical labels to the 2D fields in the x-y plot?

Line 245: Should be Table S3, not S2.

Line 383: Should be "overlying water".

Fig. 6: Please add the information about "marine" vs. "riverine" stations to the plot or legend.

Fig. 7: What do the stipple vs. solid lines indicate? Also show which sites are "marine" and "riverine".

Line 438: Should be "thus" not "this"

Line 451: This is a valid consideration rather than a confounding factor.

Line 478: Should be "may explain the observation that".

Line 517: It is not unusual that soil OM contains similar chemical signatures to the higher plants that grow and decay in them. It is perhaps misleading to state that the correlation between BIT and the EMMM results implies low contribution of vegetation input, rather it should be stated that, as you conclude later, the plant signals are transferred via the soils (where they also pick up the BIT signal).

Line 551-552: The comparison with ocean margin trends is not useful here as the reactivity gradients in near-shore areas is more likely to be controlled by terrestrial inputs than by water-depth fractionation of sinking OM.

Line 564: Remove "ancient". There is no information about age of the material so this is not relevant.

Line 567-568: Interpretation of carbonate dissolution needs to be expanded. Is there evidence for this in the data or literature? 

Line 577: The higher CH4 flux in a whole core incubation at a more freshwater site can be due to the higher position in the sediment column of the SMTZ. See e.g. the diagram in Fig. 7 of https://esd.copernicus.org/articles/13/633/2022/esd-13-633-2022.html.

Line 620: Should be "10 times faster than..."

Line 607: Check the formatting of the citation.

Line 633: Also refer to Keil et al. (1994).

Line 677-678: Separate the statements about global AOM estimates and dredging impacts, these are not obviously connected.

The manuscript of G. Wu et al. investigates the increase of organic matter (OM) degradation produced by anthropogenic perturbations such as dredging activity. The method stands on the elemental (C/N) and isotopic (𝛿13C) characterization of organic matter of 49 sites from the Port of Rotterdam. Molecular characterization was done on 13 of the 49 sites, reoxydation experiments on 6 sites and in situ OM remineralization have been estimated on 2 sites. The authors conclude from their studies that Cl#1 - CN proxies are robust to identify contribution of marine versus non-marine OM sources, Cl#2 - marine OM is more labile than terrestrial OM and Cl#3-aerobic conditions accelerates OM remineralization compared to natural (mainly anaerobic) conditions.

From my point of view, this manuscript is not reaching the quality requirement to get published in BG : the rare new knowledges brought by this manuscript are only site specific. In the conclusion, the authors underline more general concepts (Cl#1, Cl#2, Cl#3), however it corresponds to already well-established concept in biogeochemistry that does not present significant novelty.

In addition, a detailed reading of the manuscript reveal that the scientific hypothesis defended along the manuscript (that perturbation increases source-dependent organic matter degradation rates in estuarine sediment) is not properly argued. While the source characterization of the OM received large analytical efforts, and a valid interpretation supported by some modelisation, four others critical step of the demonstration seems not strong enough. First, and most important, the demonstration of a source and composition dependence of OM degradation rate is not convincing. The authors build their hypothesis from the literature and a reasonable intuition but that is in complete opposition with the dataset presented. Indeed, the two sites, selected because they present very contrasted OM origin and composition, present very similar O2 fluxes that is interpreted -reasonably- as a similar intensity of remineralization rate. This result should better be used to underline a limit of the observations from the literature. Instead, the authors use an artefact (normalization by the TOC) to build a contrast between the two stations while the relation between quantity of OM and remineralization rate have not been presented. It seems more rational to conclude from their dataset that OM quantity does not play an important role in deposit, probably because it is in large excess.

Second in importance, there is no consideration on primary production, while freshly produced algea are probably more labile than any other carbon source. In other word the local recycling of carbon between photosynthesis and respiration is neglected in this manuscript while it is probably very important in this very shallow environment. Third, while the introduction suggests a study covering many sites and embracing some spatial variability, the comparison between perturbated and not perturbated sediment is done only on 2 sediment, which seems not enough to support conclusions that could be generalized to others estuaries, and thus limits the interest of the results. Fourth, the methodology of perturbation does not seem adapted to an estuarine environment, since it corresponds to a not water-saturated sediment more adapted to mimic soil aeration than resuspension induced by dredging activities. Additionally, the dry freezing of the sediment before incubation would certainly modify the properties of the reactive organic matter – which have not been tested.