This manuscript presents the results of a field investigation of the impact of dragging an otter trawl rope across the seafloor. This is a well-designed field study that makes great use of the unique in situ observational capacities of GEOMAR. It is overall well written and structured, and will be a valuable and nuanced addition to the current literature on the impact of mobile-bottom contact fishing (MBCF) on the marine carbon cycle. One comment on the writing is that I would urge the authors to consider tempering the tone of the text – hyperbolic words such as ‘severe’, ‘dramatic’, ‘substantial’ … are used often throughout the text, but they are not necessary given the nuanced nature of the data and main results of the study. While recent publications on MBCF impacts have tended to sensationalise, this is not aiding our understanding or helping to nuance the discussion around managing MBCF. A bit more scientific sobriety would be welcome in this specific field.

I also have a few concerns and suggestions on content that probably should be addressed before the manuscript will be ready for publication. I give some general comments here, with more detailed comments below.

I believe the authors will be able to address these, and I am looking forward for a revised version of this interesting manuscript.

Kind regards

Sebastiaan van de Velde

General comments:

The main observation is an overall reduction in benthic fluxes after disturbance, which the authors suggest is due to the erosion of the surface layer with more reactive organic matter and silicates. This is very likely correct, but throughout the discussion I feel this is sometimes forgotten (see my detailed comments on L544, L609, L694). The total impact of dragging ropes on the marine carbon cycle cannot be accounted for by only measuring before and after fluxes, as the fate of the eroded layer needs to also be considered. This should be better reflected throughout the MS.

Another effect that does not receive a lot of attention is the transient nature of the data. How much of the observed change in flux is transient due to the porewater build-up after erosion/mixing event – rather than reflecting actual changes of the biogeochemical pathways? For example, the way you calculate calculation RPOC_tot from the fluxes assumes steady-state, but if you flush out the top porewater, you will get a recovery phase where fluxes will be lower until the new steady-state is reached. So your estimation of RPOC after disturbance is an underestimation. Since the large variability in SR probably means the difference is not statistically significant can you confidentally say there is a difference?

My final comment relates to the model usage and claim of pyrite oxidation. While I think this is indeed a factor that needs to be consider, I don’t see any new evidence in the manuscript that this occurs. The modelling part of the MS, which is used to claim that pyrite oxidation is important, present essentially the same model runs (with minor variations) as previously done by (Kalapurakkal et al. 2025), and thus do not validate the conclusions of the earlier manuscript, nor do they bring much new to the table, since you are essentially getting the same results. At the very least, I would have expected the field data to be used to validate the model runs, but this is also not the case.

I would suggest that the authors reconsider the added value of the model simulations in their current form (see also my detailed comment below), and also ask them to consider how these results are presented, as the sentence in the abstract at L34 and L669 give the impression that this study is an independent validation of the earlier model results of (Kalapurakkal et al. 2025), which it is not.

Detailed comments:

Throughout: ‘bottom trawling’ – is supposedly colloquial, and a more accurate term is mobile bottom-contact fishing. Not so much for the experiment in this paper, as you are looking at otter trawl specifically, but for the more broad scope papers in the introduction.

Title: might be more appropriate to name that it was an otter trawl rope

L30: ‘supresses benthic mineralization’ – the reason that happens is because a lot of reactive POC is removed – so it does not so much supress it than displace it?

L50ff – might be worth to discuss the results of (Porz et al. 2024; Zhang et al. 2024) as well in the light of the carbon sequestration debate

L82ff – I would include the papers that show/discuss the importance for pyrite formation as an alkalinity source (Hu and Cai 2011; Reithmaier et al. 2021). And it might also be interesting to bring in our recent global estimate of the chronic impact of repeated trawling (van de Velde et al. 2025) – especially since there is a first-order estimate of alkalinity loss for the area in which you did the experiment (also see the SI for a long-term reduction in TA flux due to chronic trawling). There is also an estimate of how import each individual process is for shelf sediment alkalinity generation.

L223: so you had the instruments (nutrient analyzer, alkalinity titrator, etc.) on board the ship?

L288: unclear, is this 1 to 50 or 150 or?

Section 2.8 – Curious, how does this compare to the DIC flux?

You can also do a similar exercise by including DIC and TA fluxes and making a similar mass budget, this time including carbonate dissolution and pyrite/FeS burial

Figure 4: maybe say ‘sediment cast’, which makes it easier to directly understand the figure

L432: but higher up you assume a different oxidation state for your organic carbon? Why not be consistent?

L454: lower near the surface, as they become higher at depth in the higher impact areas?

L486: why not include this in this manuscript?

L514: why surprisingly? You just describe yourself that your site is at the threshold where bottom-water O2 is controlling the O2 flux – so removing POC should not affect the O2 flux.

L518: could it also have to do with sediment type? A sandy sediment might be more prone to porewater flushing due to the disturbance, where a muddy sediment would be less. I can then see how muddy sediments would show higher fluxes right after recovery if the porewater is mixed rather than flushed out.

L533ff: are the studies you mentioned not directly determining the denitrification rates through modelling, isotope pairing, or N2/Ar fluxes? Whereas you are comparing it to the NO3 flux alone – which is not the same?

L544: I don’t think I agree with that statement – if the loss of fluxes is due to the erosion and removal of the reactive surface layer, you need to also account for the fate of that surface layer before you can make claims about the impact. If the POC gets remineralized in the water column, you still produce the nutrients, so you don’t affect the productivity.

L575: and probably most importantly: the nature of the organic matter itself (age, origin) – which to a large extent will determine its sensitivity to environmental conditions.

L590: in what way? Coarser grain size = bigger difference?

L590: Our study from the anoxic Baltic Sea suggests that low mineral protection (high OM concentrations and low sediment accumulation) leads to high mineralization rates, even under anoxic conditions (van de Velde et al. 2023; Placitu et al. 2025). This indicates that the lack of mineral protection leads to no difference in oxic versus anoxic conditions – rather the inverse of the interpretation of the results of Kalapurukkal.

Could it be that the results of Kalapurukkal actually show the effect of desorption and the age of the organic matter? Fine-grained sediments would protect OM from mineralization, meaning more reactive fractions remain. When incubated in suspension, desorption occurs in both oxic and anoxic conditions – and since more reactive OM fractions show little difference in mineralization rate under oxic or anoxic conditions (see the earlier work of, e.g., (Kristensen et al. 1995)), you observe little difference.

With coarse-grained sediments, there is little mineral protection, and the more reactive fractions have quickly reacted away. When you then incubate the sediment in suspension, the less reactive OM fractions show differences in mineralisation in oxic versus anoxic conditions.

This would lead to a slightly different mechanistical interpretation of the results and would reconcile it with our findings. It is not the grain size that controls the response of mineralization in oxic versus anoxic conditions, but grain size that controls which OM fractions are retained in the sediment – and this eventually is reflected in the resuspension experiments.

L606: also considering including our recent global estimate (van de Velde et al. 2025), and papers that discuss that sedimentary pyrite burial is an important source of alkalinity (Hu and Cai 2011; Reithmaier et al. 2021)

L609: but what about the fate of the resuspended material?

L611: ‘dramatic’ – a bit over-the-top, since you show a temporary reduction in fluxes, how does that say anything about ecosystem functioning or structure?

L612: ‘to the best of our knowledge’ – remove sentence, this does not add to the manuscript

L634: this – interestingly – is exactly the number that comes out of our global modelling exercise (van de Velde et al. 2025), and also close to the numbers of (Krumins et al. 2013). Would also be worth referencing some earlier work on carbonate dissolution in muddy sediments (Aller 1982; Green and Aller 2001)

L650: Is there no data from trawling intensity/disturbed area for the region you are studying? Would probably be worth checking (e.g., (Amoroso et al. 2018) or (Eigaard et al. 2017; Rickwood et al. 2025)) to do more realistic simulations or some sensitivity tests.

L652: So you assume no impact on carbonate dissolution? Why? It is your biggest source, and if you reduce organic matter mineralization in the sediment, you will reduce porewater acidification and this carbonate dissolution rates? Note that our model study did not find any impact, but we did not erode the top layer, but let it settle after resuspension.

L657: The way this model runs are explained are a bit confusing to me – ‘no impact’ is still impact, right? You induce mixing and get pyrite reoxidation? So the only difference with the ‘standard run’ is that you force the benthic fluxes – but are those not a consequence of the disturbance? Should you then not use your observed fluxes to validate the model, rather than run the model to upscale something which is actually not based on your observations?

L671: the paper from Kalapurakkal is a bottle incubation experiment, so I would not really say this paper shows that it happens in reality. The paper suggests that pyrite oxidation is more important that the organic matter impact – and this study seems to be a validation – or at least should be, because at the moment it seems you are using their paper to claim pyrite oxidation happens, without actually showing any data that backs that claim.

L673: but what drives that reduction in alkalinity fluxes? Pyrite oxidation should be reflected in these fluxes as well.

L694: only because you do not account for the fate of the resuspended material

L699: but you do not present evidence for the oxidation of pyrite ?

In this study, Linsy and co-authors perform a very thorough experimental study to assess the biogeochemical effects of sediment disturbance by bottom trawling in the Baltic Sea, where the authors provide valuable new evidence highlighting the complexity of such disturbance on biogeochemical pathways.

Notably, this is the first study that assesses the impacts of bottom trawling on total alkalinity fluxes from an experimental perspective rather than relying solely on modelling. It also stands out for addressing the effects of demersal fisheries from different perspectives, providing a deeper understanding of the biogeochemical consequences of demersal fisheries. By performing obtaining different sampling types (CTDs, sediment cores, landers) and analyzing a wide range of parameters, the authors provide a deeper understanding of the different biogeochemical processes affected by this sediment disturbance, while also recognizing the limitations of their approach.

I thoroughly enjoyed reading this in-depth study, and commend the authors for the work behind this. While the manuscript is both timely and highly relevant, I do have a number of comments and questions – particularly regarding the experimental design, data analysis, and its interpretation – which I hope will help strengthen the overall clarity and impact of this study.

Main comments:

1. While the description of the methodology is very detailed and could serve as a guideline for future studies that aim to better understand the biogeochemical impacts of demersal fisheries given its broad scope, it is not clear to me what kind of experimental design this study is following. I had to re-read the methods to properly identify if it was a Control-Impact experimental design, or a Before-After Control-Impact experimental design (sample all sites before the disturbance to account for temporal and site variability). I initially thought it was a Control-Impact experimental design, but when looking more closely at Table S1, I noticed that the authors also sampled the impact site before (July 19) the experimental trawl (July 20), sort of making it a BACI experimental design (only sampled the impact site before disturbance). The authors should be clearer about this experimental study design.
   
   Being a BACI experimental design, the authors should perform statistical analyses not only comparing Control-Impact, but also prior to the disturbance.
   
   In addition, the continuous sampling 16 days after the disturbance to assess the recovery is done in comparison to the control site, but it should also be done in comparison to pre-disturbance.
   
   This also raises concerns with the statistical analysis used. From my understanding, the authors combine the sediment profiles of the cores (Figs. 5-6), or the fluxes (Figs. 7) in the impact and control sites. However, since the data was collected in different periods with respect to the disturbance, which the authors plot in Fig. 8 to assess the recovery after disturbance, then combining the data assumes that the temporal variation is not relevant. A quick look at the raw data in Table S1 doesn’t show differences in the fluxes of the MUC in the impact site prior to the disturbance in comparison to the fluxes after the disturbance.
   
   The following comments assume that the data processing was correctly done, but this should definitely be looked into.
2. In relation to the statistical analyses (section 2.9), the authors consider that a p-value < 0.05 is indicative of statistically significant variability. After resolving the issue of my previous comment, I suggest the authors be more precise about the statistical significance of their results, and provide more detail about their statistical significance. For instance, the authors could add an asterisk in the figures to denote statistically significant differences with different confidence values, such as * for p < 0.05, ** for p < 0.01, and *** for p < 0.05 (or similar notation). I am surprised that there are statistically significant differences in the POC content of the surface sediment layers (Fig. 5a) considering that the limits of the error bars are touching (1 standard deviation, equivalent to 66 % of the variation of both samples). I have the similar doubts with the boxplots of TOU, TA, ammonium and phosphate of Fig. 7, since the upper and lower quartiles of the control and impact sites cross each other.
3. I am also missing some more background information of the study area, more specifically in relation to the fishing history. As pointed out in a data compilation of studies assessing the biogeochemical impacts of demersal fisheries, Paradis et al. (2024) identified that the control site in the majority of studies have been historically fished and were not being trawled during the study due to a seasonal closure or the recent establishment of a trawl ban. I am aware that the Baltic Sea has been extensively impacted one way or another (HELCOM, 2018; Bradshaw et al., 2024; Díaz-Mendoza et al., 2025), so what is the fishing history and current condition of the study area?
   
   In addition, how does the experimental fishing conducted in this study compare to the bottom trawling activities that usually take place in the Baltic Sea in terms of gear type, fishing intensity, fishing season? This is especially important to clarify and apply for the last modelling exercise (see comment 9). What is the distance between trawl tracks (red lines in Fig. 1), what is the width of the trawl nets and sweeplines? The authors have a schematic diagram of the gear type used in Figure 4, but this one is too small to annotate these elements (e..g, width between otter doors). This would be especially beneficial considering that the authors target the wide area between the otter boards (it would give additional perspective of why they target this area and not the furrows caused by the heavy otter doors).
4. The contact of demersal fishing gear with the seafloor has several effects: it can resuspend sediment and hence erode the seafloor, create furrows associated to this sediment resuspension and erosion and adjacent sediment piles, and/or mix the sediment. The magnitude of each of these impacts is difficult to quantify, and the effects on sediment biogeochemistry will differ depending on these processes.
   
   The authors observe a combination of these processes in this study: defined furrows, sediment piles next to the trawl tracks, visible scrapes, and a sediment plume implying sediment resuspension (lines 392-399; Fig. 4). What were the sizes (width and depth) of each of these features?
   
   Later on, the authors conclude that bottom trawling has removed the upper 2 cm of sediment since there are statistically significant differences of POC in the impact and control site in these surficial sections (lines 414-416, Fig. 5). However, this reduction could also be due to remineralization, or mixing of the high OC in surficial 0-1 cm with the lower OC in deeper sediment sections (affecting the shape of the POC profile). Morys et al. (2021) observe that there is an upward 2.5 cm shift in the profiles of Chl-a, OM, and water content in the impact site (IN) with respect to the control site (OUT), which they attribute to erosion of these 2.5 cm. In this study, you also determined the water content and porosity of the sediment cores. This metric could be used to determine mixing (constant porosity in mixed layers) as well as erosion (removal of the less-consolidated surface sediment as seen by Morys et al. (2021)).
   
   The different physical effect of bottom trawling (mixing and erosion) and its biogeochemical effects should be discussed in more detail. For instance, the authors relate the lower flux of nutrients in the impact site due to erosion, but it could also be caused by mixing, which would accelerate the diffusion of porewaters to the overlying water.
5. In this study, the authors identify that sediment disturbance has minimal effects on TOU, in comparison to lowered O₂ consumption rates in other studies (Tiano et al., 2019; Bradshaw et al., 2024), implying that it is the first time this has been observed. However, as portrayed in a recent compilation of biogeochemical studies of the impacts of demersal fisheries (Paradis et al., 2024), there are several other studies that have shown that there is a minimal effect of demersal fisheries in oxygen consumption (Warnken et al., 2003; Polymenakou et al., 2005; Trimmer et al., 2005; Goldberg et al., 2014; Meseck et al., 2014). These studies were done in continental margins with contrasting dissolved oxygen concentrations, so the relationship between TOU and BW oxygen observed in this study are not necessarily applicable to those other studies.
6. When discussing the mechanisms affecting the fluxes of nutrients, the authors discuss that phosphate could be released to the water column after disturbance, leading to a lower flux, but this is not the case for nitrate fluxes, since the fluxes of this latter nutrient did not vary between the control and impact sites (Fig. 7). If phosphate is released to the water column, nitrate should have been released as well (Breimann et al., 2022). Maybe the lack of significant difference of nitrate flux between the control and impact sites could be due to the counterbalance of nutrient release (as suggested for a decrease in phosphate flux) and decreased denitrification rates as reported in other studies (Ferguson et al., 2020).
7. The authors find that in the impact sites, fluxes of DIC and TA decrease. They then mention that the biogeochemical explanation for this decrease is unclear (lines 610-612). Isn’t it simply because there is a decrease in the RPOC? (Fig. 7h)
   
   Also, the fluxes of TA in this study are within the range of TA fluxes in other regions (see lines 615-616). Hence, is there really an impact of bottom trawling in terms of TA flux?
8. This is the first study that looks at the effects of bottom trawling in alkalinity fluxes. Van de Velde et al. (2025) performed a global modelling study of the effects of sediment disturbance on benthic alkalinity fluxes, and the causes behind it (carbonate dissolution, sulfate reduction and pyrite burial, denitrification). How do your observed results compare to those seen in that study? In that modelling study, they observe that the majority of the alkalinity reduction is due to changes in sulfate reduction and pyrite burial, but in your study, there are no statistically significant changes in sulfate reduction nor pyrite content. However, you mention that “sediments transition from a TA source to a large TA sink during the first trawl due to pyrite oxidation” (lines 658-659). I also don’t agree with this sentence, since the sediments do not transition to a TA sink. Their TA flux is simply reduced in comparison to the control sites, so they are simply a “less strong TA source”, to put it one way. What about carbonate dissolution? You calculate the carbonate dissolution rates in the control site, but what about the impact site? What about denitrification? See earlier comment 6.
9. Regarding the seafloor-water-air box model of the impacts of DIC and TA fluxes, I don’t understand the point of doing a trawling disturbance with and without changes in DIC and TA fluxes. The experimental data show a reduction of DIC and TA fluxes, so why make a scenario called “No impact” but still with a trawling disturbance event?
   
   The experimental approach was performed in summer, and the parameters observed during that season were applied in the box model for several years. Wouldn’t the conditions change over time? Wouldn’t the “baseline” CO₂ and TA fluxes also change seasonally?
   
   Finally, is this fishing intensity (once per year) representative for this study area?
10. Regarding future work, the authors modestly acknowledge in different points of the manuscript that they are not capable of discerning the causes behind the trends they see, and that they would need more information. What kind of information would they need to properly understand the causes behind the trends observed? For instance, the authors discuss why they don’t see changes in nitrate flux in comparison to other studies, or decreases in phosphate, DIC and TA fluxes, and mention that they would need more information.
    
    The authors also acknowledge the need to study the fate of resuspended sediment to get a broader understanding of the biogeochemical consequences of sediment disturbance. Another aspect that should be studied is the effect of repetitive bottom trawling activities. Depending on the region, fishing grounds are disrupted almost on a daily basis, which would limit the capacity of deploying landers to properly calculate porewater fluxes, especially since the authors mention that porewater fluxes could be flawed (lines 489-500). This adds to the complexity of studying the biogeochemical impacts of demersal fisheries.

Minor comments:

Line 22. The authors refer to studying the impacts on the “benthic ecosystem”, which includes benthic communities (e.g., meiofauna). However, they did not study the benthic community. I would suggest to replace “benthic ecosystem” to “benthic biogeochemical pathways” or something similar.

Line 28. Define which nutrients, since not all nutrients showed a decrease in flux.

Line 29. Change “variations” to “decreases”

Line 32. Convoluted sentence. Suggest to modify to “[…] had not returned to baseline levels by the conclusion of the 16-day observation period, indicating prolonged effects of the disturbance, although natural temporal variations may have an influence.” Or something similar.

Fig. 1. Add location of CTD deployment(s).

Lines 145-155. The authors extract porewater using two different approaches: centrifuge and Rhizon samplers. How do the results vary between both methods?

Line 221. Were these geochemical analyses performed on the same sample (the same 1 cm interval of the same core)? I’m asking this because some samples were treated (e.g., with ascorbic acid) and some were left untreated. Hence, aliquots would have had to be subsampled for each analysis, and I’m surprised you would have gotten sufficient volume for all of these analyses. Please clarify.

Lines 325-336. The diffusion fluxes were obtained from fitting the porewater data using the FindFit function in Mathematica software. As I’m not familiar with this software, and other readers may not be either, is this fitting done weighing the uncertainties of the measurement? Does this fitting give you a measure of uncertainty within a specific confidence interval? Was it error-propagated?

Figure 2. Instead of plotting wind direction on a y axis that goes from 0 to 359 (this value is cyclical), it should be plotted as an “arrow graph” (see example in Fig. 3 of Puig et al. (2003)). Another alternative would be to choose a cyclic colormap for the wind direction and use it on wind speed data (Fig. 2b).

In both Fig. 2d and e, there seems to be artifacts in the data (spikes of SST, BW Temp, and BW O₂).

The O2 concentration obtained from Winkler method in Fig. 2e is not sufficiently visible.

Finally, to give Fig. 3 a bit more context, consider adding an arrow (or similar marker) above Fig. 2 for each CTD deployment. That way, the reader will not have to find the environmental conditions during each CTD deployment in Fig. 2.

Lines 410-416. Add a more detailed description of the differences, or lack of, of POC, PON and CaCO3, as done in lines 417-418 for pyrite contents.

Line 431. Depth-integrated SRR at the control and impact sites should have a measure of uncertainty, no?

Line 468. Remove “fluxes of” in “showing the fluxes of solutes fluxes across”

Line 490. The authors mention that the two approaches have “slight differences in magnitude for TA and NH4+”. Are these differences statistically significant? And the lower H4SiO4 fluxes of BIGO, were they significantly lower?

Line 563. Add “it” in “[…] since it will affect the rates of […]”

Line 577. Remove the comma after “as well as, the local”

Line 672. The surface pyrite content in the impact and control site are not statistically significantly different.

Line 676. Sentence is missing a verb

Finally, I am also looking forward to read the future studies that will come out from this group (lines 486-488 indicate that more work is currently being undertaken by the group).

Regards,

Sarah Paradis

References in this review

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