Bartl and Thrush conduct experiments to gauge the amount of additional CO2 released from sediment disturbance using incubations of natural sediments sampled from Hauraki Gulf, New Zealand. The authors analyse their results using a machine learning method and find non-linear relationships and interaction effects between additional CO2 release and sediment characteristics. It is concluded that assessments of carbon storage vulnerability must account for sediment heterogeneity.

In general, the paper is well written, and the methodology clearly described. However, I found the current presentation and interpretation of results to be lacking. The fact that sediment heterogeneity needs to be accounted for when assessing carbon impacts is already well-established (and somewhat trivial), and the usefulness of the resuspension assay has already been introduced in the earlier work by Bartl et al. (2025). The results of the BRT model are interesting, but they are presented in a quite condensed manner, and it is not laid out clearly what exactly we can learn from them.

I do think the data collected and the experiments done are valuable and useful, but the discussion focuses almost exclusively on the BRT results, which are difficult to interpret, since such ML methods tend to obfuscate possibly straight-forward interactions and relationships. I encourage the authors to dig a bit deeper into their data through additional analyses and/or to present the BRT results in more detail, and to discuss the possible mechanistic explanations for the observed patterns. I list some specific suggestions below, along with other comments.

General comments:

• The resuspension assay is meant to mimic trawling impacts, but it’s not clear what the historical and current trawling intensity in the study area looks like, or what other bottom-disturbing activities (dredging, sand mining, …) may occur in the study area. Can the authors give some additional information about this in 2.1? Right now, it is only briefly mentioned in the introduction.
• The assay is based on SOD measurements, which are then converted to CO2 based on a constant RQ. The authors have justified this choice in Bartl et al. (2025), but I am not convinced that this should hold for this analysis as well. Is the value of RQ=0.9 valid for every sampling location? How can the authors be sure that their measured SOD is due purely to OC mineralisation, as opposed to aerobic oxidation of other species, which has been shown to be a larger oxygen sink in some muddy sediments compared to OC mineralisation (e.g. Kalapurakkal et al., 2025)? Perhaps the authors can give some information on oxygen penetration, redox-depth etc. in their samples to clarify this.
• Only absolute SHAP values are shown in Fig 2A+B even though, according to 169-172, positive and negative impacts of each feature can be distinguished by the sign. For example, I would expect OM:Phyto to have a negative sign. This important information is hidden by showing only the absolute values. Also, can metrics like SD or ranges, (based on the 50 iterations of the model and/or based on the mean of iterations but for all data points) be shown for the SHAP values to get a sense of their distribution/uncertainty?
• The authors focus their discussion on the results of the BRT model, but the interpretations of the resulting patterns and their mechanistic explanation is lacking. For example, two mechanisms that immediately come to mind are (1) decreased oxygen penetration in muddier sediments that could decrease OM degradation upon resuspension and could explain the disproportionate RCO2P compared to sandier sediments and (2) a decrease of terrestrial OM with distance from coast could explain the pattern in Fig 2D, assuming that terrestrial OM is generally less labile in marine environments compared to marine OM. Terrestrial vs. marine OM is mentioned briefly in 2.1, but it is never discussed afterward, though I assume it should have an impact on the degradability. Can the jumps/non-linearities (Fig. 2) be separated geographically, e.g. between firth, channels and offshore? This could be a straight-forward explanation for the patterns shown in the BRT results. Another question that is not addressed is why M-Sand should have such an important role (though it’s not clear why the authors focus on this fraction in the first place, since it seems to be no more important than the other sand fractions; see specific comment).

Specific comments

• 1: The authors may consider adding a larger-scale, regional map to give readers unfamiliar with the area a better sense of where the area is located.
• 14-15: „…we quantified RCO2P and it with measurements of sediment grain size, organic…“ missing word?
• 28: I suggest adding references to some other studies to give a sense of the large uncertainty in this number (e.g. Epstein et al., 2022; Hiddink et al., 2023; Zhang et al., 2024).
• 2: Though details may be provided in Bartl et al. (2025), a short description on how the resuspension assay was performed would be helpful (e.g. using only the top 3 cm, gentle shaking, …)
• 117-119: The naming of the combined sand size classes is a bit unfortunate as it could create confusion, so I suggest introducing the acronyms “F-Sand” and “C-Sand” here and using those whenever referring to the combined classes, rather than “fine sand” and “coarse sand”.
• 137+231: remove comma after „Both“
• Tab 1: I don’t see Phaeo:Chla in the table, though it’s defined in the Table description.
• 175-177: Can the authors be more specific here? Which features could be omitted for the prediction? And doesn’t this clustering imply that the interactions are not so important, and that OM itself is already a quite good predictor?
• 177-178: M-Sand does not seem to be more important than the other sand classes according to Fig. 2a. Why do the authors choose to focus on M-Sand, and how can the high interaction score of M-Sand with OM be explained? The short discussion in 249 (“…other environmental factors play a role for the reactivity of sediment OM and thus RCO2P”) is quite unspecific.
• Fig. 2C-E: It may be worth drawing a zero-line in these plots
• 211: The authors may consider removing the linear regression formula here, since it disrupts the flow for the reader and is already included in the description of Fig. 3.
• 240-241: Which range is being compared here to arrive at 2-88 mmol/m2/d? The range of undisturbed CO2P from Table 1 (0.1-1.0 mmol/m2/h or 2.4-24 mmol/m2/d) is different.
• 248: “median” should be “medium”
• 250: Looking at the supplemented maps, it doesn’t seem like grain size is always decreasing along the depth gradient. Maybe the authors can rephrase to clarify what is meant here.
• 254: I don’t think it’s fair to say that the study has found any “interactive dynamics” at this stage, but rather relationships; the dynamic process understanding needs to be explored further.

References

Bartl, I., Evans, T., Hillman, J., Thrush, S., 2025. Simple assay quantifying sediment resuspension effects on marine carbon storage. Methods Ecol Evol 16, 309–316. https://doi.org/10.1111/2041-210X.14479.

Epstein, G., Middelburg, J.J., Hawkins, J.P., Norris, C.R., Roberts, C.M., 2022. The impact of mobile demersal fishing on carbon storage in seabed sediments. Glob Change Biol 28, 2875–2894. https://doi.org/10.1111/gcb.16105.

Hiddink, J.G., van de Velde, S.J., McConnaughey, R.A., Borger, E. de, Tiano, J., Kaiser, M.J., Sweetman, A.K., Sciberras, M., 2023. Quantifying the carbon benefits of ending bottom trawling. Nature 617, E1-E2. https://doi.org/10.1038/s41586-023-06014-7.

Kalapurakkal, H.T., Dale, A.W., Schmidt, M., Taubner, H., Scholz, F., Spiegel, T., Fuhr, M., Wallmann, K., 2025. Sediment resuspension in muddy sediments enhances pyrite oxidation and carbon dioxide emissions in Kiel Bight. Communications Earth & Environment 6, 156. https://doi.org/10.1038/s43247-025-02132-4.

Zhang, W., Porz, L., Yilmaz, R., Wallmann, K., Spiegel, T., Neumann, A., Holtappels, M., Kasten, S., Kuhlmann, J., Ziebarth, N., Taylor, B., Ho-Hagemann, H.T.M., Bockelmann, F.-D., Daewel, U., Bernhardt, L., Schrum, C., 2024. Long-term carbon storage in shelf sea sediments reduced by intensive bottom trawling. Nature Geoscience. https://doi.org/10.1038/s41561-024-01581-4.

Bartl and Thrush carried out replicated manipulation experiments of superficial (3 cm) sediments obtained from a total of 57 sites in the Hauraki Gulf (New Zealand) characterized by varying edaphic characteristics to estimate CO2 release due to resuspension. The study poses foundation on an early manuscript (Barts et al. 2025 Meth Ecol Evol) describing the resuspension assay and how this could provide an estimate of the vulnerability of marine sediments ability to store carbon when exposed to bottom disturbance and applies it in the field at a basin scale.

Using machine learning methods, and after the removal of collinear explanatory factors, they identified organic matter (OM) content (but not its freshness), sand contents and water depth as the factors most influential on the CO2 release from the manipulated sediments. Based on these results and using scatter heatmaps, the authors identified values of the explanatory factors representing thresholds of vulnerability to CO2 release by sediment resuspension. According to those thresholds, a large portion of the sediments of the Gulf under scrutiny show from moderate to high attitude to releasing CO2 when disturbed. The authors conclude that the assessment of the vulnerability of marine sediments ability to store carbon must account for sediment heterogeneity. Ultimately, the authors prompt that sediment heterogeneity must be accurately considered when deploying plans of spatial management of demersal fisheries (one of the most disturbing anthropogenic factors on the sea bottoms).

The paper is well written and easy to read. The premises in the introduction and the logical flow that brought the authors to the study design are both clear. The methodology is clear as well (but see below for some missing details) and the data analysis conducted rigorously. The results highlight the most important insights obtained from the experiments. Nonetheless, some issues emerge dealing with the description and reliability (or possible biases) of the resuspension assay and with the discussion, which is limited and provides the analysis only a small portion of the other (not considered factors) possibly explaining (>40%) of the CO2 release variability. The discussion, as it is presented now, opens more questions than the answers (though credible) the study provides. I’m convinced that the effort in doing this study and the potential of the obtained results can be conceivably more properly and deeply discussed.

I’m convinced that this study deserves publication and the information it includes could become a starting point to include sediment heterogeneity among the factors to be considered when planning demersal fisheries, but it needs a larger effort to discuss more affordably the strengths and the weaknesses of the presented results.

Below I provide some suggestions to improve the manuscript.

The putative role of sediment heterogeneity on the effects of impacts (including the natural ones) affecting the sea bottom is somewhat obvious. This, however, has been not considered in deep by science nor policy making. Despite the authors declare it, a deeper and more accurate description of the potential implications of considering it is not anticipated in the introduction, nor extensively addressed in the discussion.

The manipulation method used for resuspending the sediment in this study derives from an early paper published by the same scholars’ team. Despite they prompted in the former article “Depending on the research question, we recommend trials with local sediments to determine optimal incubation times, core sizes, and sediment to water ratios”, no mention of these important data is provided in the manuscript. How much this affects the observed interactions? Moreover, other important details about the resuspension assay are missing, which obliges the reader to jump between the two papers for these details, that could be added in a supporting methodological file. This, obviously, does not prejudice the validity of this manuscript. Nonetheless, either in the former paper or in this manuscript, there is a possibly relevant bias: the energy employed to resuspend the sediment was apparently the same for all samples (“The jar was topped with filtered seawater, sealed airtight and gently inverted for 30 s. The sediment-water mixture was left to settle for 30 s, the jar was re-opened and the initial oxygen concentration was measured”). Considering the ample variety of grain size composition of the manipulated sediments, this could represent a possible uncontrolled simplification.  This appears a possible not irrelevant bias: since sediment grain size is tightly related with its compactness, different sediments are differently impacted by the same amount of energy. This means that the simulated resuspension cannot represent the mechanic impacts of trawling on sediments with different characteristics. In this sense, the authors can use their results only to discuss the effects of a severe resuspension on sediments, but without providing a comparison of the energy used to simulate resuspension and that causing the resuspension by the “average” trawl, the results cannot be effectively translated into possible demersal fishery management plans accounting for sediment heterogeneity.

In the methodological paper the authors identify different RQ constants, but here they used only one. Is this correct? Is there any possibility to distribute better this constant?

The lack of a control with OC-free sediments would have helped to clarify whether the CO2 production measured in the resuspended microcosms depends only from OC mineralization. I see this now is unfeasibly corrected, but a possible bias from this should be acknowledged.

The authors used the OM:Phyto ratio as a proxy for OM freshness. They referred to a paper in which the authors, however, used the percentage fraction of phytopigments and biopolymeric C (which does not account for total OM). This, honestly, does not modify the significance of its “new” use, but should be acknowledged.

The lack of information about the composition (and origin) of the OM in the sediments makes difficult making any generalization. The authors acknowledge that different proportions in labile and refractory components could lead to different reactivity to osygen of OM. Nonetheless, this issue needs to be discussed more deeply.