Review to Monsoonal influence on floating marine litter pathways in the Bay of Bengal

General comments

This manuscript deals with the connectivity of floating macro-plastics released along the coast in the Gulf of Bengal. This region seems to be an under-sampled and under-studied area from a Lagrangian point of view. In this way, the results of this manuscript are of interest. The manuscript is clear and well written. The approach of initializing Lagrangian scenarios uniformly along the coasts to overcome the major uncertainties in source estimates is interesting. However, there are some limitations and important methodological points that need to be addressed to finalize the study before it can be published.

From the plastic problem point of view, I regret the country-by-country approach of this study, which leaves each country to its own responsibilities instead of promoting collaborative regional approach as it is recommended by scientists and NGOs in the context of current international negotiations for a treaty against plastic pollution. For example, countries upstream of watersheds share the responsibility for marine pollution, and measures must be discussed with continuity at borders to ensure fairness towards countries with long emitting and accumulating coasts (such as Myanmar designated in this study). A alternative in future work would be to segment the coasts according to ocean dynamics or sub-region land use or coastal types.

I suggest adding a limitations section to the methods and/or discussion. We understand that the authors use Ocean Parcels by activating the options already coded in the tool. However, the processes chosen and activated should be at least described and discussed, mentioning particularly their limitations. It is important to be able to interpret the results in the light of these uncertainties. The 2D approach, for example, that might over-estimate the beaching rates (no undertow for mass conservation as in 3D) should be discussed, as does the simple addition of Stokes drift to 2D Eulerian currents (no anti-Stokes force created contrary to coupled simulations).

Moreover, the manuscript is based on comparison of stranding between two simulations with different resolutions. Even if 2 km is a high resolution for regional approach, neither of the two runs has sufficient resolution to represent coastal and beaching processes, the dynamics in the coastal grid cells will still be very different (as mentioned by the authors in the section 4.3 but unfortunately not showed with figures). I suggest that the authors need to further clarify the particle release strategy in the two simulation, depending on the size of the grid cells, which is decisive for the comparison of beaching statistics (a figure zooming on coastal cells of both simulations with the particle release locations would be welcome, as well as one showing the final locations when they are considered beached in both simulations). This would illustrate how the resolution numerically constrain the release scenarios and beaching statistics, in addition to the representation of the dynamics.

Detailed comments

L33. “Despite the large uncertainties”: this is very important in the current challenges of quantifying sources and monitoring plastic pollution in the marine environment, I suggest to add the orders of magnitude of these uncertainties here referring to the recent literature on the subject (interesting studies have followed the precursory but not up-to-date study by Jambeck et al., 2015).

L41. “with fewer looking at the connections of litter that ‘beaches’, or washes ashore, along coastlines”: seems exaggerated, many studies have indeed focus on the gyres, well represented by the large-scale dynamics, whereas coastal processes are more complex but there is still a significant literature on Lagrangian tracking applied to plastic beaching issue. An updated state of the art would be welcome.

L42. “two-thirds [...] is captured on coastlines”: I suggest to note the huge uncertainties in the statistics mentioned here given the resolution of the global models cited.

L59. “Lebreton et al. (2017), which have very high uncertainties”: others river input models have shown the sources of uncertainties in the mentioned reference, add citations

L93. “Stokes drift [...] wave motions”: How is added the effect of Stokes Drift on the 2D current fields? A simple addition is physically very different from a coupling process for example

L95. “Windage [...] trajectories”: for which macro-plastic size are these 1% consistent ? Is there a risk of obtaining excessively high drift velocities for particles by combining all these effects?

L114. “Particles [...] locations.”: did the particles have exactly the same release lon,lat in both simulations given the different resolutions of coastal cells and the same distance to the land mask?

L122. “weightings could be applied [...] future”: this perspective may be little excessive, the number of particles released per day seems low and the question of statistical representativeness of the diversity of possible trajectories is not addressed (“500 coastal locations every day, [...] with 182,500 particles released in total”). The authors should add a statistical sensitivity test to show that the number of particles released is sufficient to represent the diversity of particle fates in the studied region (i.e. increase the number of particle releases and see if it changes or not the connectivity statistics, taking into account the spatial and temporal variability of the dynamics - in the same way they have done the temporal resolution sensitivity analysis described in Appendix A).

L150. Are the 100 particles really released at exactly the same position and at exactly the same time? So why do the 100 differ from one another? 

Figure 2. It would be interesting to be able to see the weekly particle clouds (like Fig. 2b) for each D1-4 drifter trajectory in the supplementary materials, to see the spread associated with the statistics in Fig. 2c (for each of the two simulations). Also, does Fig. 2b correspond to CMEMS or ROMS advection? Please specify.

L192. It would be welcome here to have, for example, a current map to understand why the exit patterns are different, and based on the bibliography of dynamics in the region, which seasonal pattern is predominant over the years. I did not find the corresponding circulation analysis in the Discussion section.

L243. The fact that beaching is predominant in the vicinity of source points in all literature studies at these modeled resolution does not confer an element of validation since none of these studies allows the representation of realistic beaching. I would advise more nuance with regard to the numerical limitations in these assertions, especially as the study's beaching criterion is rather simplistic.

L267. The quantification of connectivity between countries seems totally linked to particle emission scenarios, the argument brought by the authors at the end of the section is in fact central to the differences observed compared to Chassignet et al., 2021 and should be mentioned right at the beginning of the paragraph: the sink differences should be discussed in relation to the differences in sources of the cited publication (in term of quantity and location).

L282. I was not able to see the Supplementary animations. I suggest that this section 4.2 could be illustrated by one or two figures of ocean circulation to help understand the different seasonal pathways discussed and the importance of simulation resolution for the study of connectivity.

L335 - 339. The assumptions made here should be illustrated by coastal zoom circulation maps (eddies and/or offshore current) at the two simulation resolutions used. Otherwise remove as unfounded.

L341. Has the CMEMS product assimilated the drifters' profiles? If so, it's normal that the CMEMS simulation corresponds better to the observations even if its resolution is coarser.

L360. Even with Stokes drift and windage included in the study, coastal processes are not represented: put more nuance in this sentence. Moreover, Stokes drift seems to be added by simple addition with the Eulerian current fields: here again, this is a strong limitation to be discussed. In coupled simulations, Stokes drift forcing creates a feedback from the current fields called anti-Stokes force that attenuates the total current compared to the total current obtained by adding the Eulerian current and Stokes drift without coupling at each time step.

L380-383 Same remark as in the method section. To ensure that the conclusions drawn from the study's Lagrangian simulations can be extended to different cases by weighting the particles according to various source scenarios, I suggest adding a sensitivity test in the appendix showing that the number of particles released is sufficient for the connectivity obtained to be statistically representative: a comparison of the spread and connectivity of clouds composed of different numbers of particles with slightly different time and space initialization should be added (with a histogram as in Fig. 2c for example).

L400. “Our simulations [...] litter.” This recommendation is far too vague and should be removed: targeting the entire Myanmar coast is illusory, and the study offers no way of targeting smaller coastal transect suitable for the scale of a beach litter observation.

L404-405. Same comment as above, the present connectivity study remains interesting, but the scale of the coastline considered here is not suitable as support for policy decisions and beach cleaning operations (which requires a link to finer scales). I suggest nuancing the last two sentences or removing them.

Appendix A. L433. “The differences in sink locations [...] negligible”: I would put more nuance into this kind of statement, the connectivity presented here is calculated between very long lengths of coastline, if smaller transects had been taken into account for the connectivity study, the differences might be higher.

Figure A1. Rather than giving the difference between the two connectivity matrices for each simulation, give the percentage error

Main comments

This study concerns the dynamics of floating plastic waste in the Bay of Bengal based on particle tracking simulations. Using a uniform release of particles along coastlines in the Bay of Bengal, the authors find that most particles beach in their country of origin and that the seasonally reversing East India Coastal Current (EICC) is the main driver of particle transport in the region. The study is relevant, and the manuscript is well-written and has high-quality figures. I have two main comments, which I believe can be addressed with additions and clarifications to the manuscript text and figures, with perhaps some additional analyses.

My first main comment concerns the approach to beaching in the study and, as an extension of that, the release locations. Since the connectivity between countries in the Bay of Bengal is determined based on beached particles, I think the assumptions and limitations of the beaching method should be thoroughly discussed in the manuscript. The authors mention in the Discussion that their “model accounts for several processes … key mechanisms thought to drive the beaching of floating particles, such as windage or Stokes drift”. They also discuss that the higher resolution ROMS model likely incorporates coastal dynamics more accurately than the global CMEMS model. While I agree with both these points, I think it is important to note that:

1. Although the ROMS model may have a higher resolution and may capture coastal dynamics more accurately than the global CMEMS, both the Stokes drift and wind fields are based on global models and have coarse resolution (I assume ~25 km, although this is not specified). Since these are the mechanisms that are responsible for ‘beaching’ in the simulations, I think it is important to clarify that these are unlikely to represent fine-scale coastal dynamics and therefore are probably not capturing accurate beaching dynamics of floating particles.
2. The beaching of particles is not simulated explicitly in this study, instead particles simply become stuck on land if they end up on a coastline (approximated in the study by identifying near-zero velocities rather than using a land mask). Since there is currently no consensus on the correct way to simulate beaching, I do not necessarily have an issue with this method, but I think the authors should make this clear in the manuscript. There are several studies that use different (probabilistic) approaches to beaching (e.g. Onink et al. 2021; Irfan et al. 2024; van der Mheen et al. 2020b; all already referenced in the manuscript); it would be good to briefly mention the different approach in these studies and explicitly clarify the approach used in this study in the Methods.
3. I think it is also important for the authors to clarify whether it is possible for particles to become stuck on land because of ocean currents (which is sometimes the case when ocean currents are interpolated incorrectly along coastlines but is not physically valid) or because of the random motion of particles, or if they implemented some method to only allow particles to end up on land as a result of Stokes drift and windage (which, as the authors also mention in the Discussion, would be the only physical mechanism to result in beaching). If no method was implemented to ensure this in the simulations, it would be useful if the authors could provide an indication of how many particles may become stuck on land (in areas on non-zero velocity) due to model artifacts (e.g. ocean current interpolation and random motion) versus due to Stokes drift and windage, though I appreciate this may be difficult to determine. In addition, the authors use the condition that a particle’s velocity is close to zero to determine if a particle has beached. I assume that wind velocities have been set to zero above land? Since the land boundary is effectively identified by zero velocities, does this mean that “land” (or the area of zero velocities) is formed by a combination of the different velocity fields at different resolutions (rather than, for example, taking the land mask from just the ocean current models)? It would be useful to briefly explain this in the methods, and if “land” is indeed identified as a combination of all velocity fields, I think it would be useful to show maps (perhaps in an Appendix) of what this looks like for both the CMEMS and the ROMS simulations.
4. Regarding the release locations: I think using a uniform release along coastlines is an excellent method to gain insights into the dynamics of floating plastic in the region, especially (as the authors also highlight) given the large uncertainties surrounding estimates of riverine and coastal plastic sources. However, I do think that the choice in release location (distance from the coast) may have an effect on the simulation results, especially since the emphasis is on the beaching of particles. I think the motivation of releasing particles away from the coast (to not release any on land) but still in the continental shelf region (to hopefully capture some coastal dynamics, rather than only open ocean dynamics) is the correct one. However, in the Methods it is mentioned that “this distance was chosen to complement different coastlines from the two hydrodynamic models”. Considering that the coastlines from the hydrodynamic models are not actually used as “land” to determine beaching, I am not sure if this is the correct motivation. I do not necessarily think that this needs changing in the simulations, but I think the wording here gives the impression that the ocean current models determine where beaching will occur, which (if I understood correctly) is not the case since the Stokes drift and wind field velocities also contribute to this. I would recommend showing maps with both the release locations and the zero-velocity “land” that is determined with the combined velocity fields (assuming that the land boundary shown in Figure 1 is a general boundary and not based on the zero-velocity region). Releasing close to the coast and considering the high beaching percentages on countries of origin also raises the question how many particles end up on land shortly after their release (see also my second point for this).

In addition to clarifying the points above in the manuscript, I think at least a paragraph in the Discussion should be dedicated to discussing the limitations of the simulation methods, with a particular focus on the beaching method. I think a discussion of the dependence on beaching on fine-scale local dynamics (which I think are unlikely to be captured in these simulations, despite the higher resolution ROMS model) should also be included. Some potential references for consideration for this are, for example: Pawlowicz et al. (2019), https://doi.org/10.1016/j.ecss.2019.106246; Zhang et al. (2020), https://doi.org/10.1016/j.scitotenv.2020.136634; Hinata et al. (2020a), https://doi.org/10.1016/j.marpolbul.2020.110910; and Hinata et al. (2020b), https://doi.org/10.1016/j.marpolbul.2020.111548.

My second main comment concerns the discussion of the seasonal variations results (section 3.3). Figures 3c-h show connectivity matrices for particles released during the monsoon, post-monsoon, and pre-monsoon but beaching at any time during the simulation. Figure B1 shows the same connectivity matrices but for beaching only occurring during the specified monsoon season. I am not sure that Figure B1 should be in an appendix. I think showing both the connectivity matrices for beaching throughout the simulation and for beaching during the relevant monsoon season is important. For example, in the results for the monsoon season the authors identify that “the second highest beaching rate was always on a country in the anticlockwise direction” in Figure 3c, which does not make sense to me during the monsoon season, since the currents are in a clockwise direction. In Figure B1a this pattern doesn’t seem to be as pronounced (e.g. second-highest beaching of particles from India is in Bangladesh rather than in Sri Lanka, which seems to make more sense with the direction of the ocean currents during the monsoon season). The connectivity matrices during the post-monsoon season in Figure 3 and Figure B1 also seem quite different. I think it is important to discuss these results along-side each other, as they can also provide information about how many particles tend to beach within the same season versus during a following season. Similarly, the mention of the different boundaries through which particles exit the region during the different seasons is interesting, but it does raise the question during which season these particles exited the region (not just in which season they were released).

In addition to showing the connectivity matrices, I think it would also be very relevant to show timeseries of the percentage of particles beaching and exiting the region (e.g. different panels per season release and different colours per country release). This would provide insights into how many particles beach very quickly after their release, within the same season of release, and in a different season.

Minor comments

I appreciate the validation of the ocean models with the undrogued drifter trajectories. However, I think it is important to make it clear from the start that these drifters provide validation in the open ocean only and not in the coastal ocean (where you may expect the higher resolution ROMS model to perform better than CMEMS). The authors make this clear in the Discussion, but I would recommend also briefly pointing this out in the Methods and Results sections about the validation. I would also be careful about including this in the Abstract, I personally think the sentence “Both simulations were validated using the pathways of undrogued surface drifters, with better agreement found for particles advected by data-assimilated ocean velocity” misses some nuance and may be misinterpreted.

The terminology around the monsoon seasons is a bit inconsistent throughout the manuscript (e.g. use of spring, summer, winter in the Introduction; pre-monsoon, monsoon, and post-monsoon in Methods, Results, and Discussion; Northeast Monsoon, Southwest Monsoon, Winter Monsoon in Discussion). I would recommend defining the pre-monsoon, monsoon, and post-monsoon seasons in the Introduction (the monthly definitions are now only given in the Methods). Since there is some different terminology used around the monsoon seasons in the region, it would also be beneficial to include the specific months you are referring to in all Figures and the Table.

I would appreciate some discussion about the choice of using ocean surface currents + Stokes drift + 1% windage to represent the transport of floating plastic waste. It is mentioned in the Methods that 1% windage best represents the effect of wind on drifters (undrogued?) but is there evidence that these drifters behave as floating plastic would? I do not have an issue with the choice of forcing fields, but I do think the choice should be discussed more. For example, while this may represent the transport of many very buoyant plastics (all but the largest, as mentioned in Methods), this may not correctly represent less buoyant or smaller plastics drifting at, or close to the ocean surface. I was hoping to see a sensitivity analysis on different forcing mechanisms, at least with and without windage added. It would be very interesting to see how this affects beaching in the simulations, but I appreciate this may be out of scope for the current study.

Please mention the temporal resolutions of the ocean models in the 2^nd paragraph of the Methods as well as the horizontal resolution. This is briefly mentioned later in the Methods, along with a vague reference to sensitivity tests in Appendix A. I think the temporal resolution is important, and the choice to use daily-mean (or is it daily intervals?) velocity fields rather than hourly velocity fields is non-trivial. This should be clarified and discussed up front. Regarding the sensitivity tests in Appendix A, while I do not think that these are critical to the manuscript and its results, I am afraid that I do not find the tests themselves very convincing. Looking at the particle positions in CMEMS, these are quite different between the daily and hourly resolutions (though the ROMS positions are remarkably similar, and interestingly the CMEMS daily positions seem to more closely resemble those from ROMS). Since the sensitivity simulations were only run for a month, I don’t think using the beaching connectivity matrices is a valid justification for using the daily resolution. Perhaps a comparison between hourly and daily particle trajectories (as was done with the validation against drifter trajectories) makes more sense here? It is also not clear to me why the authors prefer to use daily velocity fields when hourly ones are available? I think there should be some justification for this, and it should also be mentioned in the Discussion as a possible further limitation to capturing coastal dynamics relevant to beaching.

Please also mention the horizontal and temporal resolutions of the Stokes drift and wind fields in the 2^nd paragraph in the Methods.

Please note that, in addition to Chassignet et al. (2021), van der Mheen et al. (2020b) also identified country-to-country connectivity. It may be worth adding a comparison to those results as well (currently only a comparison with particles exiting the region is done, not country connectivity). Alternatively, I would briefly mention that van der Mheen et al. (2020b) also includes this country-to-country connectivity and explain why no comparison with these results is done.

In the Discussion (L380-383) and Conclusion (L402-405) the possibility of weighting particle releases based on future improved source estimates is suggested. I personally think it unlikely that this would be done, it seems more likely that simulations would be rerun with more particles released from relevant sources, especially since running particle tracking simulations is relatively accessible and not very computationally costly. I suspect the authors mention this possibility to justify the uniform release (there is quite a lot of emphasis on justifying this throughout the manuscript), but I think this release is already well-justified because it allows a focus on the dynamics of floating plastic waste in the Bay of Bengal without having to deal with uncertainty surrounding source-estimates.

In the Abstract (L23-26) and Conclusion (L404-406), I personally think that the results of this study are generalised a bit too strongly. I would say that the main results of this study are that most simulated floating plastic beaches in its country of origin and that the EICC seems the main driver of plastic transport in the Bay of Bengal. Perhaps some more general conclusions can be drawn from this, for example that countries preventing plastic waste entering the ocean will benefit from reduced plastic waste washing up on their own shores, but I would not say that this study can be used directly to target beach clean-ups and aid policy decisions. I would suggest a bit more nuance in both the Conclusion and the final sentences of the Abstract.

Figure 1: Can you add the months to the “Pre-monsoon & monsoon” and “Post-monsoon” labels in the figure? Is it possible to also add a general direction for the wind/Stokes drift to the schematics here?

Figure 2: Panel a shows “a snapshot of ocean speeds from the ROMS dataset”. Please add the date used for the snapshot.

Can you make the coloured dots in the legend of panel a larger? Please also check if the colours chosen are suitable for different colour vision deficiencies.

Perhaps consider adding a “start” and “end” marker to each of the drifter trajectories (of the overall trajectories only, not the weekly portions for validation).

I appreciate the drifter trajectory with the particles in panel b. Are the particles for the CMEMS simulation? Would it be possible to show the same for the other drifters as well (perhaps in an Appendix/as supplemental figure)? D4 may be very chaotic to show, but I would be interested to at least see D1 (lowest MCSD for the ROMS run) as well as D5 (lowest MCSD for the CMEMS run).

Table 2: Please add the months to the monsoon seasons as well. Also, perhaps consider “Full simulation” instead of “Year”?

Should this be Table 1?

Figure 3: Please also add the months to the monsoon seasons above the connectivity matrices here as well. Consider “Full simulation” instead of “Year” for the top panels.