The study at hand seeks to attribute the mortality impacts over the UK and the Nordics of the sudden stratospheric warming event in February 2018. To do so, the authors combine state-of-the-art methods from weather prediction modelling with an epidemiological impact analysis. The approach of attributing impacts of single weather events is novel and might help preparing societies better for these consequences. I further want to congratulate the authors on a very clearly written paper that is well structure and thus easy to follow.

My major concerns are about the epidemiological analysis and its application, the use of monthly data for estimating temperature-mortality relationships, and the application of the different temperature datasets. My review focus is in the health impact analysis, as I'm no expert on stratospheric processes. I’ve also included some minor comments, that caught my eye whilst reading the draft.

• Epidemiological analysis I

To my understanding the authors first fit a model that expresses the expected mortality as a function of (daily mean, I assume) temperature. However, in environmental epidemiology, temperature attributable mortality is calculated differently (see Gasparrini, 2014). Attributable fraction of mortality is calculated as

AF = (RR(T) − 1) / RR(T)

where AF stands for attributable fraction and the RR for relative risk from the DLNMs. Temperature attributable numbers of mortality are then subsequently calculated as

                  AN = n * AF

Where n denotes the number of cases (daily deaths, on that day). To be more precise, you could also use the (forward looking) running mean of n, with the number of lag days (same number as lags within the DLNM) as duration.

Directly estimating cold-attributable mortality from the relative risk, as I suspect the authors are doing here, would thus lead to a strong overestimation and is technically incorrect.

• Epidemiological analysis II

Several recent studies use a two-stage approach (i.e. Sera, 2022) two improve the estimate of the coefficient by pooling the spline parameters of the DLNM. This would likely improve your counterintuitive results of the RR curves for some locations as displayed in Figure 7 (i.e. where the curves bend downward again at very cold temperatures). There are several studies with open code which you can use for mimicking the methods (i.e. Vicedo-Cabrera, 2021).

• Epidemiological analysis III - DLNMs for weekly data

The authors state that applying DLNMs to weekly data is not trivial. However, this is routinely being done (i.e. Ballerster et al. (2023)).

• Epidemiological analysis IV – binning methods

While I acknowledge that there is an advantage of using several statistical approaches to estimate temperature-related mortality – I’d suggest restricting the analysis to the standard DLNMs here, as this should not be an epidemiological methods development study. Also, I don’t think that it is appropriate to use monthly data for estimating temperature-mortality relationships, as the short term effect of individual days are important. Otherwise, I’d suggest to quantitatively compare models based on their AIC score, and not qualitatively as currently done.

• Epidemiological analysis V – country level and monthly data

Again, I’d suggest to sticking to standard epidemiological methods, as otherwise you should show a clear model intercomparison (local vs. district/country vs. country level results, daily vs. weekly vs. monthly data, model assumption, model parameterization, etc.). The argument of using country level and monthly data for Nordic countries is not very convincing to me, as there certainly are daily mortality counts somewhere (at least there is published literature on it).

• Temperature data applied
  
  
  
  I see two concerns with the temperature data – I don’t think it’s adequate to use a country level mean as input to the epidemiological analysis, especially for Finland, where a vast majority of the population is concentrated around Helsinki. I’d suggest using a population weighted temperature time series. Same could be done on a county-level. But then again, I don’t think that a country wide assessment is suitable in the first place.
  
  
  
  The spatial resolution column in Table 3 is not very helpful (for me at least). Could you maybe express everything in degrees (as being done for the CESM2)?
  
  
  
  It is quite important that the temperature distribution of the model data corresponds to the distribution with which the temperature-mortality relationships are calculated, otherwise you might include a model-bias in your impact calculation. This can be done i.e. using quantile mapping as a bias-correction method.

Minor comments

• Section 3.3 is a bit of a blend of results and discussion, yet is listed within the Method Section
• Page 11 – typo: “..exposure-response curve with strongly depend..” (with instead of will)
• Page 13: MMM (I assume mulit model mean) – I think it’s the first time that this acronym appears within this manuscript
•  

Gasparrini, A., & Leone, M. (2014). Attributable risk from distributed lag models. BMC medical research methodology, 14(1), 55.

Sera, F., & Gasparrini, A. (2022). Extended two-stage designs for environmental research. Environmental health, 21(1), 41.

Ballester, J., Quijal-Zamorano, M., Méndez Turrubiates, R.F. et al. Heat-related mortality in Europe during the summer of 2022. Nat Med 29, 1857–1866 (2023). https://doi.org/10.1038/s41591-023-02419-z

I really enjoyed reading this manuscript on comparing the DLNM approach with the binning approach. It is a well-performed and well-written analysis and points to a useful approach if high-resolution data is not available. In some parts it was very, very detailed, on the other hand, it showed well how the authors conceptualized their alternative approach and how they planned to show its usefulness compared to the more common approach using DLNM. 

I only have two questions as I mostly know the DLNM approach. To my knowledge, one advantage also lies in the fact that one can in addition adjust for further environmental factors which occur at the same time as the extreme temperature exposure, e.g. adjustment for humidity or air pollution. I assume that this would not be possible for the binning approach? Especially with these stratospheric and tropospheric conditions described in the paper, maybe also the accumulation of air pollution , similar as in inversions, could contribute its share. 

My second question is on the population offset that can be used in DLNMs in case you look at a population over a longer time period. The population could increase or decrease and therefore this automatically leads to more or less death counts (e.g. also the percentage of the susceptible population could change). People sometimes account for that with an offset for each year in the model. Would that also be doable with the binning approach?

And one technical point: The reference on page 12, line 232 should be "The Eurowinter Group", not just "Group".

This study aims to attribute excess mortality in the UK and Nordic regions to the 2018 SSW using stratospherically nudged ensemble forecasts. Exposure-response curves are derived using historical near-surface temperature data and mortality data and are then applied to the ensemble forecasts to calculate expected deaths in the 30 days following the 2018 SSW. I really enjoyed reading this study and thought that it was novel, well-written, and the figures were high quality and clear. I have only a couple of comments regarding the meteorology of the study.

Firstly, the ensemble experiments used in this study use stratospheric zonal mean nudging at 90 hPa and above. Are the results of this study sensitive to the level at which the nudging is executed? Additionally, is the nudging of the stratosphere gradually increased to full nudging at 90 hPa to ensure that edge effects do not occur? Please clarify.

My other comment is regarding the interpretation of the results. If I am not misunderstanding, the estimated mortality risk and excess death data is based on the difference between the nudged and control simulations. I therefore think it is very important to ensure clarity when describing the results, because the mortality statistics are therefore expected statistics based on how the model evolves at the surface in response to nudging. For example, there is the statement that says "We find that about 750 deaths in England and Wales were attributable to the impact of the February 2018 SSW" in section 285. However, surely this is expected deaths based on the ensemble predictions? Given that the mortality estimates are derived from model-simulated differences in temperature responses to stratospheric nudging, the results support a conditional, model-based expectation rather than a direct attribution. I recommend revising this wording throughout to explicitly reflect the conditional and expected nature of the estimate.