The manuscript by Zhang et al. uses a 1-D coupled sea ice-ocean model to examine the impacts of meltwater on sea ice melt and upper ocean stratification. Sensitivity analyses were run to compare how the percent of meltwater changes the upper ocean stratification and sea ice melt/formation. The authors compare stations across the Arctic, from the strongly  stratified Canada Basin to the weakly stratified Nansen basin. This is a novel and important study that sheds light into how stratification and sea ice melt are closely coupled. There were however some gaps in the research and some confusing wording, which I will explain below. I think this manuscript can be published in Ocean Science after moderate revisions.

Major comments

My first major comment is that important details were left out of section 2. Specifically, I was left wondering the following:

1. How long were the simulations run for?
2. Why were only data for short periods in April or May used for initialization?
3. What time step was used for the simulations?
4. Why were no data used for initialization between 2014 and 2020?
5. Why was the MLD definition selected? See Peralta-Feriz and Woodgate (2015; Seasonal and interannual variability of pan-Arctic surface mixed layer properties from 1979 to 2012 from hydrographic data, and the dominance of stratification for multiyear mixed layer depth shoaling - ScienceDirect) for an overview of different MLD definitions in the Arctic

My second major comment is that there was no discussion about how heat released from the NSTM melts ice through winter. A number of studies (Winter sea‐ice melt in the Canada Basin, Arctic Ocean - Jackson - 2012 - Geophysical Research Letters - Wiley Online Library; The impact of stored solar heat on Arctic sea ice growth - Timmermans - 2015 - Geophysical Research Letters - Wiley Online Library; Episodic Reversal of Autumn Ice Advance Caused by Release of Ocean Heat in the Beaufort Sea - Smith - 2018 - Journal of Geophysical Research: Oceans - Wiley Online Library) have shown that strong stratification can store the NSTM through winter. This heat can be gradually released throughout winter via storm-driven mixing, which breaks down the stratification. Evidence of the heat release can be seen by ocean to ice heat fluxes. I wonder if including ITP data from the winter of 2007-2008 – a year where the NSTM was stored year round – would change the results in Figure 5c?

My third major concern confusion with the feedback language used -  in general, I got confused with how the authors were referring to a negative and positive feedback in this context. I think adding some clear definition of negative and positive feedbacks in the introduction as well as how these feedback are related to the atmosphere-ocean-ice- system would help the readers understand the importance of these results and how they fit into previous knowledge.

My fourth major concern is that knowledge from several important manuscripts were missing. In addition to the above cited manuscripts, I suggest the authors read the following:

1. Toward Quantifying the Increasing Role of Oceanic Heat in Sea Ice Loss in the New Arctic in: Bulletin of the American Meteorological Society Volume 96 Issue 12 (2015) (ametsoc.org)
2. Modeling the formation and fate of the near‐surface temperature maximum in the Canadian Basin of the Arctic Ocean - Steele - 2011 - Journal of Geophysical Research: Oceans - Wiley Online Library
3. Winter Convection Transports Atlantic Water Heat to the Surface Layer in the Eastern Arctic Ocean in: Journal of Physical Oceanography Volume 43 Issue 10 (2013) (ametsoc.org)
4. Freshwater and its role in the Arctic Marine System: Sources, disposition, storage, export, and physical and biogeochemical consequences in the Arctic and global oceans - Carmack - 2016 - Journal of Geophysical Research: Biogeosciences - Wiley Online Library
5. Arctic sea-ice melt in 2008 and the role of solar heating | Annals of Glaciology | Cambridge Core

Minor comments

• Section 2.1 – I find this section confusing the way it is written. Specifically, the variables were not described in the order that they appeared so I had to jump around to understand. I suggest reorganizing so that the variables are described. Another option is to add a table that lists and defines all variables.
• Line 74 – What are the estimates of vertical diffusivity in the Canada Basin versus the Nansen Basin? I imagine vertical diffusivity is smaller in the Canada Basin due to the strong stratification. I suggest the authors add a sentence that cites studies that have examined vertical diffusivity from different regions to justify their decision to choose this parameter value.
• Line 81 – Why were these values chosen for albedo. Pleas add some references to justify this choice.
• Figure 1 – I can’t see A5 in this figure.
• Line 99 – Why is ITP E6 not listed here?
• Lines 112 to 114 – The NSTM is defined based on salinity and it looks like the temperature maximum in A1 to A3 shown in Figure 2 include both NSTM and Pacific Summer Water. I suggest adding this to the Figure 2 description.
• Lines 178 to 179 – I think the authors have made an error here. They state that the MLD was deeper in the western Arctic than Eastern Arctic. I think here they define the western Arctic as the Canada Basin? Please clarify.
• Section 3.1.1 – While the model does a good job of reproducing the NSTM, the modeled NSTM is colder than the observed one, which could have implications for sea ice melt and formation. Could the authors please add a few words about how the colder NSTM could impact their results?
• Lines 196 to 203 – Previous literature (e.g. Figure 5b in Jackson et al., 2012; Figure 7 in Smith et al., 2018) show observational values of ocean to ice heat flux, including episodic high values in the Canada Basin in winter. I suggest the authors compare their results with these studies.
• Figure 6 – Why is there only 1 station from the Canada Basin?
• Lines 234 to 240 – How do these results compare with results from Peralta-Feriz and Woodgate, 2015?
• Figure 11 – It is difficult to distinguish the line colours. Also, as mentioned above, I find the wording of positive and negative feedback to be confusing.
• Figures 12 and 13 – I found it confusing to decipher what positive and negative values mean. It would help the reader if you added this to the figure caption.
• One suggestion I have for future research, which could be added as a sentence in the discussion, is to add wind sensitivity experiments to explain how wind mixing impacts the stratification and sea ice melt/formation.

This is my first review of a paper titled ‘A numerical study on meltwater feedback in the coupled Arctic Sea ice-ocean system’ by Zhang e al. The paper discusses the impact of freshwater from sea ice melt on sea ice growth/melting itself. Using a 1D sea ice - ocean model the authors find that depending on the initial stratification, the meltwater has a strong negative feedback on ice melt, but depending on stratification can have either a positive or negative impact on the following winter ice growth. The results themselves are interesting, although I do question the linkage to meltwater alone (see below). As such the manuscript lacks some details and could be published with minor revisions, although the results reflect the importance of freshwater in general, not meltwater alone. However, I give suggestions to modify their experimental setup to actually attribute their results to sea ice meltwater, or to carry out with their results, but to recast their results in terms of general freshwater perturbations. I encourage the authors to consider the suggested modification to their approach and therefore suggest major revision.

Major comments:

1) If I understand correctly, what the authors do here, is that they have one ‘control’ simulation with full meltwater release and perturbation experiments with scaled down versions of meltwater release. However, although the amount of meltwater release is scaled down the sea ice melt itself stays the same, i.e. some freshwater disappears in the process.

Because the authors also don’t take into account any other sources of freshwater, the influence of sea ice meltwater in respect to other freshwater sources remains unclear. To me, the experiments, as thry are done now, appear more as traditional freshwater release experiments (albeit with seasonal cycle), rather than experiments that would try to isolate the role of sea ice meltwater. If the authors would want to really isolate the role of sea ice meltwater on the ice melt/growth, then I think one would need to do something like this:

• a) Create a simulation that reproduces ITP profiles with other freshwater fluxes included. Based on Figure 4 the authors claim that this is the case already, but the simulations done here are very short and already at the surface mixed layer the salinity differences can be several PSU in some stations. The easiest would be to deduce freshwater convergence from ITPs and remove the (observed) sea ice melt water flux from the convergence, allowing the model to calculate that. It would also be interesting to diagnose the actual sea ice melt water flux from ITPs and for example cross-correlate that with sea ice growt accross the different ITP's to see if the authors hypothesis can be identified in the observations.
• b) Once the authors have the stable control simulation, they could repeat the experiments, keeping the freshwater convergence the same, but perturbing the sea ice meltwater flux.

Such an experimental setup would answer the question ‘what is the importance of sea ice meltwater for sea ice melt/growth?’. In the current setup I would argue that all the authors can truly answer to is ‘what is the role of freshwater for sea ice melt/growth (thermodynamic)?’. I do think the identified feedbacks are neat, but in the current form I think the authors would need to rephrase their aim, and discuss the caveats of their experimental setup. For example, in their 0% experiment, there is no freshwater source to the surface, which obviously gives a very large signal, but it is not realistic to claim that this signal can be attributed to sea ice meltwater (because there would be other freshwater sources contributing to the stratification). I leave it to the authors to decide on their approach, but I would think modifying their setup would be achievable and would certainly increase the impact of the paper.

2) L74 in the model description the authors write that the sea ice package is based on viscous-plastic sea ice model. Although this is true, perhaps there should be a sentence specifying that in 1D case the dynamics don’t play a role (or do they?) and the ice growth is determined by thermodynamics alone.

3) Ice thickness initialization to 2.5 m is an idealization (of multiyear ice), and that is fine as such, but I’d imagine the simulations are relatively cheap to do so I wonder if it would be worth repeating the experiments with thinner initial ice (something that represents first year ice). I would think that most locations in the Eurasian basin rarely have 2.5 m thick ice these days.

4) Similar to the comments by the other reviewer, the model experiment need to be better documented (when are they initialized, how long are they run for etc.). Some of this information is in discussion section, but that comes far too late for the reader.

5) I would change the order of discussions and conclusions.

Figure 3: are the labels in f and g correct, or should they be the other way around?

Figure 5 and other similar figures: I would encourage the authors to show anomalies from a control case instead of the full values (it is hard to appreciate the differences at the moment).