The paper uses a dynamic modelling approach that accounts for the different extreme total water level components (mean sea level, tides, storm surges, waves) and some of the non-linear interactions between them. The analysis is performed using one way coupling of a 3D ocean circulation model which captures MSL, tides, and meteorological surge and a wave model (forced with the same atmospheric data and considering water levels from the ocean circulation model). The analysis is conducted for the period 1970 to 2100 and non-stationary extreme value analysis is applied and compared to results from using the simplified “static” approach (or “MSL offset method"). Given the important of changes in extreme coastal water levels in driving changes in coastal flood risk, the analysis adds valuable new insights in terms of which methods are suitable in which regions. I add some major and several minor comments below which need to be addressed to make the manuscript publishable.  

Major:

• One big concern that I have is about the uncertainties in the extreme value analysis, which are crucial since they are used to identify regions where the static and dynamic approaches lead to different results. There is no explanation of how uncertainties in the distribution parameters and resulting return level estimates are derived; is it the Delta Method, or Bootstrapping, or something else? Overall, the uncertainty estimates appear unrealistically small and that would lead to more places being identified where static and dynamic approaches are “different”. Looking for example at Figure S1.1 the uncertainties in the 100-year water levels (derived from ONLY 20 years of data) are only a few centimeters in some of the places and maybe 10-20 cm in others for the static approach. They become a bit larger in the dynamic approach because the shape parameter changes signs, but especially for those unbounded distributions the uncertainties are usually very large, particularly when GPD is fitted to short records (as is done here). I don’t think this can be correct and would mean that all the conclusion regarding “significant” differences between static and dynamic approaches are corrupted. I am not sure if maybe some uncertainties were ignored (like the ones in the shape parameter) or not propagated properly (as in the Delta Method), but something is off. I know the authors say they use the tool that was already published but that doesn’t mean it does the right thing. The reason I give “major revision” is because this is a critical point that may change the results/conclusions.
• Calafat et al. (2022; https://doi.org/10.1038/s41586-022-04426-5) showed that trends in storm surges are comparable to trends in MSL at several coastline stretches in Europe and that this has led to pretty large changes in return periods. This clearly challenges the conclusion which is also drawn here in line 370 that “changes in ESL primarily depend on SLR”. They also showed that small ensembles cannot capture the full picture of ESL changes. I would like to see some discussion about how the results presented here relate to that.

Minor comments:

19 “significant” in a statistical sense? If so which significance level? If not ina statistical sense I suggest changing and not using the term in a paper like this where statistical significance is also a big part

34-37 what about freshwater discharge?

97 return levels

115-120 Would the model resolve changes in (coastal) tides as a result of SLR or is it too coarse?

137 after runoff there is a closing bracket but no opening one

153 types

173-201 Somewhere it should be highlighted that a “direct” method is used which fits the GPD to the still water levels which include (often large) deterministic tide signals as opposed to the more appropriate “indirect” methods such as SSJPM where the stochastic surge/wave part is analyzed with the extreme value models and combined with the tides.

198 see my first major comment, it needs to be explained how those confidence levels are derived exactly

Fig. 2 Is that a real example or just (used as) a sketch? If it’s a real example it would be good to mention whether it uses the static or dynamic approach.

242 The German Bight is equally (if not even more) complex than the Dutch coast.

266 This seems to be quite relevant, what is the reason for not including it in the main manuscript?

Fig. 4 Related to my point about uncertainties it would be interesting here to show the ranges of years including the distribution uncertainties and also see where those ranges overlap between SSPs and where they don’t

278 This related to my comment above about changes in tides and whether they can actually be resolved along the coast

325 lead to

The manuscript presents a dynamic modelling approach for simulating extreme total water levels, while also accounting for non-linear interactions between the different components. For this purpose the authors combine a 3D ocean circulation model and a wave model for the period 1970 to 2100 and compare the results to, what the authors term, a static approach to provide new insights regarding the potential of dynamically estimating changes in extreme sea levels. The paper is interesting, well written and the methods appear to be robust. I do however have a few comments/questions that the authors should address before the manuscript is published.

1. It is unclear to me how the uncertainties in the return level estimates were estimated. The authors should further elaborate on this point as it is also important for assessing the differences between the static and the dynamic approach.
2. The authors state that they validated the 1 in 10 year return water level instead of the 1 in 100 year. From an impact/risk assessment perspective however the latter is potentially more important. I therefore believe that the authors should further report on the validation of the 1 in 100 year water level.
3. The authors have employed the empirical Stockdon et al. model for estimating wave contribution. Besides several assumptions associated with the use of this model, the authors have assumed a constant beach slope of 4% (note that Hinkel et al., 2013, used a global value of 2% for estimating erosion). Considering that there are several other datasets (which the authors actually cite) and the fact that one could even use land slope as a proxy, I find the use of a constant slope value a little oversimplistic. The authors have commendably performed a sensitivity analysis to explore the effects of their assumption; nevertheless, if I am not mistaken, the figure in the supplementary material suggests substantial differences (both in absolute values but also in patterns) depending on the chosen value (unless I am misunderstanding something). I think the authors should further elaborate on this point.
4. Line 258 – I find the argument that the replication of the north-south gradient is enough to indicate that the single forcing GCM is “to some extent” representative of the projected changes rather weak. Also, “to some extent” is very vague.
5. The authors conclude that changes in ESL depend on changes in MSL, with coastal contributions having a lesser effect. Considering that some important parts of the coast have not been considered, can the authors really generalise this conclusion based on their results?