This study analyzes the role of diurnal vertical migrations performed by micronekton (fish, crutaceans and cephalopods) on the biological carbon pump. The authors developped a simple model describing explicitly the vertical movements of the animals as well as ingestion, respiration and the production of fecal pellets. The model relies on three state variables which are the biomass of the preys, i.e. mesozooplankton which do not perform DVM, the biomass of the consumers and the gut content. The latter variable is necessary to accurately describe the production of fecal pellets. The consumers are visual predators meaning that they need light to capture their preys. During the night, they reside near the surface to feed. At dawn and dusk, they swim to stay at depth during the day so that they escape predation from their visual predators. In the model, temporal variation in the light levels triggers DVM. The model is run in constant as well as seasonnally varying environmental conditions. It is used to explore the role of size and taxonomy on the DVM patterns and its impacts on the active vertical transport of carbon. Detailed sensitivity analyses are performed by systematically exploring the parameters space. The main findings are: (1) in the temperate regions, DVM is responsible for an important vertical transport of carbon from the euphotic zone to the mesopelagic domain; (2) Size and taxonomy play a big role in driving this transport; (3) There are strong seasonal variations of this active export of carbon with a maximum reached in summer; (4) Results are very sensitive to some parameters, such as the vertical swimming speed, the metabolic rate and its sensitivity to temperature.  

This study adresses an important topic which is increaslingly acknowledged as an important component of the biological carbon pump. The modeling framework is relevant as it includes the essential aspects of the animal physiology and it explicitely simulates the vertical movement of the organisms. It remains simple enough so that detailed sensitivity analyses remain feasible and can be applied to a large range of environmental conditions, except probably in the polar regions (polar days and nights). It is well written, even if as a non-english native speaker, I am not necessarily the best person to judge this aspect. Supplementary materials are interesting and bring some important additional information to the manuscript. However, I have some serious issues with the study, mainly with the model description and modeling assumptions. As the code is available on a github server, I have closely inspected it to check what is stated in the manuscript. 

First, there is an issue in the system of equations 1. Specific dynamic action is a respiration term and thus, represents a loss of carbon. However, this is not included in the system despite the fact that it is routed to inorganic nutrients (equations 6). I checked the code to see if this corresponds to a bug but this is not the case as it is properly taken into account in the temporal evolution of the C biomass. This should be corrected since before I checked the code, I thought that the manuscript was relying on bugged results. 

Second, the daily evolution of light is said to be described by equation 1 of the supplementary materials. This equation is difficult to read because the exponent n should apply to the sin function and not to wt. Furthermore, this equation implies that light levels are zero at night meaning that visual predators cannot feed at night when they stay close to the surface. The only available temporal window in that case is during dusk and dawn (about 2-3 hours a day). However, during that period, they move either up or down which implies that they are not colocated with their preys. Thus, according to that equation, they should not really be able to feed and they should starve and die. Yet, this is not the case. I was also disturbed by figure 2 which shows the daily evolution of light at the surface. On that figure, the relative light level during the night is not zero as it should be according to the equation displayed in the supplementary materials but somewhere between 0 and 0.6. I inspected the code and saw indeed that the actual coded equation is not exactly that of the supplementary materials but rather equation 1 to which a constant 0.5 is added. This explains why the consumers are able to survive in the model since with this 0.5, they are then able to feed at night. However, this 0.5 implies that light level during the night is about one third of its value during the day, which is obviously not correct! In addition, the Beer-Lambert equation is used with an attenuation coefficient of 0.001 m^(-1), meaning an attenuation depth of 1000 m! In very clear water, the coefficient is rather of the order 0.02-0.03, which is at least one order of magnitude higher ... This is not a typo because this 0.001 is the actual value used in the code. And the option to use a chlorophyll dependant coefficient is not activated and not included in the call to the beer-lambert function. To conclude with my issues on light, once in the manuscript and once in the supplementary materials, the authors say that day length at the winter solstice is 6 hours and is 12 hours at the summer solstice. This is obviously incorrect as day length at the summer solstice should be 18 hours.

Third, in the supplementary materials, the authors shows results from some sensitivity results on the seasonal variations of temperature, light and PP (which is in fact phytoplankton biomass rather than PP). This is very interesting. Yet, I don't understant the changes they impose on the parameter C_alpha. In scenarios 1 and 2, this parameter is set to 3 but when light is seasonally varying (scenarios 3 and 4), it is set to values that are between 2 and 3 orders of magnitude lower. Yet, the resulting detritus biomass is similar. Furthermore, the chosen values in that second case are not consistant with figure S8. Weird!

Fourth, I don't understand why the authors have added a remineralization term in the fecal pellets equation (equations 6). Are the detritus pools prognostic variables or simply diagnostic variables? I did not check the code for that specific aspect. What do the authors call the production of fecal pellets? Is it (1-e)dG or (1-e)dG -r(T)D_g? Why including this remineralization on fecal pellets but not on dead organisms? Why only remineralization and not vertical sinking which, for organisms of that size, is way more important at controlling the concentration than remineralization? This needs to be explained and discussed. On the topic of production, I don't understand what is displayed in Figure 7a. If this is the temporal evolution of detritus production, then the units are wrong. If this is the temporal evolution of the detritus pools, this is impossible since the animal dead bodies and the inorganic pool do not have a sink term. This is also the case in Figure S4. And as a biogeochemist, I was a little bit disurbed by the definition of the pe-ratio which traditionnally is the ratio of the export at some depth over PP whereas here, this a ratio between a flux and biomass. 

I had some more minor points but considering the main issues I listed above, I think they are not really relevant at this stage. I did not make any comments on the results and discussion because of the concerns I had on the model formulation which according to me, raises questions about the validity of the results. Regarding the results, one intriguing observation is the occurrence of small, localized peaks in the production of dead bodies between the epipelagic zone and the depth at which organisms reside during the day. What could explain these peaks?

In conclusion, while this study shows considerable potential, it is not ready for publication in its current form. The authors need to revise certain aspects of the model formulation and provide clearer justifications and descriptions of their choices to ensure that the results are robust enough to support the subsequent analysis.

        

General comments

The authors present a 1D numerical model designed with a theoretical parameterization of micronekton diel vertical migration (DVM) to evaluate its influence on the biological carbon pump. This simplified framework allows for an in-depth exploration of how environmental factors—such as primary production, light levels, temperature, and seasonality—along with intrinsic characteristics of different micronekton populations, including respiration rates, swimming speed, and assimilation efficiency, affect the vertical distribution and transport of organic carbon. The model explicitly simulates the vertical movements of micronekton and their feeding behaviors, including ingestion, assimilation, respiration, and fecal pellet production. The model operates within a spatio-temporal dynamic, incorporating prey-predator interactions where visual predation drives predator behavior, with micronekton migrating to the surface at night to feed and descending during dawn and dusk to avoid predators. DVM is triggered by changes in surface irradiance, with DVM dynamics varying according to micronekton size and taxonomic groups. To isolate the effects of different groups, the authors conducted simulations for each taxonomic group independently, avoiding any interactions. Sensitivity tests were performed to assess the impact of metabolic parameters on model outcomes. Key findings include (1) the significance of considering both size and taxonomy when modeling the Mesopelagic Migration Pump (MMP); (2) the crucial role of accurately estimating respiration rates to reduce uncertainties in MMP simulations; (3) greater micronekton-driven particle export in the mesopelagic zone during summer and at deeper depths due to daylight activity; and (4) the strong influence of respiration rates on the variability of model outputs across different taxonomic groups.

One of the less-studied components of the biological carbon pump is the MMP, which contributes significantly to carbon flux. While most research has focused on zooplankton, the role of micronekton in the present-day carbon budget remains poorly quantified. This study addresses an important gap in our understanding and is highly relevant to marine ecology. What stands out in the modeling approach is the incorporation of physiological traits specific to different taxonomic groups, adding a useful dimension to the analysis. However, I believe the model remains somewhat theoretical due to the lack of data for validation. Incorporating net sampling and acoustic data, if available, would be crucial for calibrating and validating the model outputs. The authors mention the presence of trawl and acoustic sampling data from the APERO cruise, conducted in the same region during June and July, but it is unclear whether these data were used for model validation. This would be a key step to enhance the reliability of the results. 

I would also like to have clarifications for the choice of 200 m depth as the euphotic zone for calculating the efficiency of particulate organic carbon (POC) transport. Most studies typically use a depth of 100 m for the euphotic zone, so it’s important to explain the reasoning behind your choice of depth. Was this depth based on specific data from the PAP-SO station, or was it taken from existing literature? The selection of the depth threshold for the euphotic zone is critical, as it can significantly affect the calculated efficiency of POC transport. If not well justified, using 200 m instead of 100 m could potentially skew the results, leading to over- or underestimation of the POC transport efficiency. The export efficiency is usually calculated using the flux at a specific depth over the net primary production, what does integration phytoplankton concentration in the surface layers represent? is it a biomass? 

Although the current model is a simplified 1D water column setup,  the authors made several assumptions and choices in their study’s design to assess the role of the DVM of micronekton on the organic carbon budget. One significant assumption is that mesozooplankton do not migrate and are restricted to the epipelagic layer, which could influence the estimated carbon flux. Numerous studies, including those by Kiko et al. (2017, 2020), and Bianchi et al. (2013), have demonstrated that zooplankton also exhibit DVM and that they are usually present between 300–600 m. Incorporating a portion of zooplankton in the deeper layers of the model would be important, as they could serve as prey for micronekton, potentially contributing to fecal pellet production and, in turn, to carbon transport. Another issue concerns the environmental variables influencing DVM. For instance, oxygen concentration plays a crucial role, especially when micronekton inhabit oxygen minimum zones (OMZs). In such zones, low oxygen availability limits respiration and metabolic rates, impacting vertical migration behavior. However, the model assumes that micronekton feed exclusively at the surface, without considering the potential effects of hypoxic conditions on DVM patterns and metabolic processes, this might be due to the modeling of the PAP-SO station. But factoring in these environmental constraints could offer a more nuanced and accurate representation of micronekton's contribution to the carbon cycle and would make the model fit to be globally applied to a large range of environmental conditions such as the Atlantic OMZ.

Another concern I have is with the light in the model. The equation in the supplementary materials assumes that surface irradiance is zero at night, which is not entirely accurate. Even at night, there is still some ambient light (e.g., from the moon), and predators that rely on visual predation may still be able to feed, albeit less effectively. The current model restricts feeding to dusk and dawn, which is problematic since micronekton are supposed to be migrating between surface and deeper layers during these periods. According to this assumption, predators would be unable to feed and, over time, would likely starve. However, when examining Figure 2 in the manuscript, it appears that surface light never actually reaches zero, contradicting the assumption in the equation. This inconsistency suggests that something might be missing or oversimplified in the supplementary equation. Could it be that the equation does not fully account for low-light conditions at night? is there a missing parameter to this equation? Additionally, have you considered varying light levels to simulate different migration depths? 

A few small comments concern these two points: I am also unclear about the changes imposed on the parameter Cα and why even though it varies between the scenarios we still have the same resulting detritus concentration. Could you provide further clarification on how the cα was modified and why such large differences do not lead to corresponding changes in detritus biomass? In equation 6, it is unclear to me, if remineralization only applies to fecal pellets or if the author considered it also in the dead organisms, considering that both processes would contribute to organic matter degradation, so excluding remineralization for dead bodies seems inconsistent. 

In conclusion, while this study holds significant potential, it still needs additional work for it to be published. The article could benefit from improvements in the clarity of idea presentation and the explanations behind methodological choices. The authors should validate the model, as this is essential for ensuring the robustness of the results. They also need to refine the treatment of light, zooplankton migration, remineralization, and detritus dynamics, and resolve inconsistencies in parameter adjustments. 

References: -Bianchi et al. (2013) doi:10.1002/gbc.20031

-Kiko et al. (2020), doi: 10.3389/fmars.2020.00358

-Kiko et al. (2017), DOI: 10.1038/NGEO3042