The study by Fahad et al. aims to explore the stratospheric temperature response to external forcing. To this end the authors analyze a series of 30-year perpetual time slice experiments with forcings corresponding to year 1992, 2000, and 2020 conditions. The authors motivate their study with a stratospheric temperature increase during 1992-2000 and decrease during 2000-2020. While I appreciate the authors aim to advance our understanding of stratospheric temperature trends and variability, I identify a series of shortcomings in the presented work.

Specific Comments:

1) The time periods for trend analysis: the authors motivate their analysis with opposing trends between 1992-1999 and 2000-2020. I consider the first time period too short for a robust trend analysis. Similar positive sloping trends could be randomly identified e.g. at the end of the time series in Fig. 1b. Overall Fig. 1 highlights strong inter-annual variability in the temperature evolution over the Arctic polar cap. To provide further insights into the drivers of this variability – and its peak amplitudes – would be a worthy endeavor and I suggest the authors to focus their analysis on this rather than short-term trends or tendencies.

2) Simulation design and ensemble size: the authors investigate 30-year perpetual simulations with 1992, 2000, and 2020 conditions. Each year of these simulations is treated as single ensemble member that are pooled for composite analysis. Generally, I consider this ensemble size too small to derive robust conclusions especially, given the large inter-annual variability in NH polar cap stratospheric temperature. Commonly single forcing studies focusing on stratospheric temperature effects have utilized 100 year (+) plus integrations. How robust are the findings against sub-sampling? How different/overlapping are the polar cap temperature distributions across these 30-year sets? How would the results change if a bootstrap analysis is applied?

3) How robust are the findings against the starting years selected?

4) How does the vortex state and stability in these integrations compare with the observational record? And how different is it within and across the ensembles?

5) In analogy to comments 2+4), how different are the EHF (and stationary and transient terms) within these integrations? How robust are the findings against bootstrapping?

6) The study is based on ensembles obtained with a single model, which does not particularly well align in terms of variability (trends and their significance) with reanalysis data (as shown in Fig. 1). I would suggest including in a revised manuscript additional models to corroborate the results.

7) The authors refer several times to supplementary figures, which I could unfortunately not find enclosed in the preprint or linked to a research square.

The paper investigates the recent decadal variations of the polar stratospheric temperature during boreal winter (DJF) by analyzing the last 30 years of reanalysis datasets, simulations of a 1-degree ocean-atmosphere coupled GCM (GEOS-MITgcm) and CMIP6 historical simulations. Two types of simulations are performed with the coupled GCM, some are forced with time-evolving CO2, ozone and aerosols from 1992 to 2020 and called transient simulations. Some others have constant concentrations of CO2, ozone and aerosols related to a given year and called "perpetual year" simulations. The authors detect a positive trend in polar stratospheric temperature from 1992 to 2000 and negative trend from 2000 to 2020 in both the ensemble mean of the transient simulations and reanalysis. They also show that the "2000 perpetual year" simulations have higher stratospheric temperature than the "1992" and "2020 perpetual year" simulations. The setup of the "perpetual year" simulations is interesting to investigate the stratospheric temperature changes during the last decades. However, no physical interpretation of the results is provided. The heat fluxes budget show that wave propagation and breaking does play a role. But there is no interpretation of why waves behave as they do for the different experiments. So the paper does not provide any direction of why 1992, 2000, 2020 generated different behaviors in the waves. I have another major concern related to the detected trends. Computation of trends is quite strange when analyzing 8 consecutive years from 1992 to 2000. I think these trends for this small period are not significant (in particular ERA5 in Fig.1b or high-top simulations in Fig.8b). Also from a statistical significance point of view, it would be important to show the spread of the 30 members in Fig.1a to see if the ensemble means are significantly different. To conclude, even though the perpetual year simulations are interesting, the paper does not provide any interpretation of the different behaviors of the three years 1992, 2000, 2020 and there is a strong lack of significance tests. How do the various changes in CO2, ozone and aerosols influence the waves and residual mean circulation ? Such a question should be adressed in the paper but this is not the case. Therefore I recommend rejection of the paper even though I must admit there is some potential for publication in the future but with an entirely revisited paper including deeper analysis of the simulations and an interpretation of CO2/ozone/aersols effects. 

Major concerns:

I) About detected trends. In fig1.b, interannual variability is very large compared to the trends. The results of the detected trends for the first period (1992-2000) might strongly change if the year 2000 is included or not. Same thing in Fig.8b, by removing or adding a year for the high-top simulations, the sign of the detected trends might change. 

II) Significance tests. In addition to I) about trends, we do not know if the difference between the 30-year ensemble means are significantly different. Please show all the members, or least add the max and min among all members.

III) Section 3.2 is entitled "dynamical mechanism of forced change" but I do not see any interpretation of why the waves could change their propagation and breaking as function of the different forcings. So in my opinion, there is no proposed mechanism to explain the observed changes in temperature and waves propagation. All the figures from 2 to 7 are consistent with each other but this only provides a part of potential mechanims to explain the changes.

IV) Simulations. The authors mention several times that the changes cannot result from low-frequency modes of interannual variability but they do not show any evidence. Line 102, the initial states are said to be uncorrelated but which variables have been looked at ? SSTs ? Also it is not clear to me if the 30 initial states are the same for the P1992, P2000 and P2020 simulations.

V) Abstract. I found the abstract not well written. It should first mention decadal variations in reanalysis and results of the transient simulations before desribing the "perpetual year" simulations. Analysis of heat fluxes cannot be called "analysis of the temperature budget (line 13) since a full temperature budget would require to show the diabatic terms too.

VI) Wording. In some sentences, the text contains too strong statement. For instance, line 249 "high-top simulation" is said to be "very similar to reanalysis and GEOS-MITgcm simulations". I do not think the trends of the first period exist in reanalysis (Fig.1b) or high-top simulation (blue curve in Fig.8b) and that the curves resemble to each other. Another example is in line 283-284 "The opposing polar stratospheric NH temperature trends in the two periods examined here are only significant during boreal winter". Why is the word "significant" used here ? In Fig.1 I do not see any significance tests.

VII) Supplementary information. I was not able to download it from the web sites.