General comments

This manuscript quantifies, and aims to improve, the predictability of sudden stratospheric warming events using statistical methods. The contribution is significant and valuable, as the authors manage some impressive improvements in predictability while keeping the machine learning physically constrained and transparent. The data processing pipeline is simple enough to be reproduced, which is not always the case with similar studies. They also exercise care in checking the robustness of their results with cross-validation. I do have some technical questions and concerns about some "hyper-hyper-parameters", in particular the motivation for the SSW definition. Provided these choices are explained, the paper should be suitable to publish after minor revisions.

Specific comments

1. My first and primary concern is with the data-driven index for slow-recovering SSWs. My understanding is that you opted not to use a standard definition, e.g., the reversal of zonal-mean zonal wind at 60N and 10hPa as per the WMO, for two reasons: (1) to have a continuous sliding scale, and (2) to avoid arbitrariness. However, you could easily modify the WMO definition to make it continuous, e.g., by changing the zonal-wind threshold or the duration. Also, standard definitions enjoy the significant advantage of being simple and objective, whereas data-driven methods such as the one you describe (PCA on temperature profiles) seems to require far more arbitrary choices, such as the size of the polar cap region, the pressure levels, and the spatiotemporal resolution. You do back up your choice by citing multiple preceding studies linking the temperature profile with surface impacts, so I'm not asking you to change the procedure, but the standard definition could be dealt with more thoroughly. I would hope that many key conclusions of the study, such as statistically significant precursors, would not change much if you were to swap in the standard definition. However, you do refer to the standard criterion at various later points in the paper; overall, I was unsure to what extent the WMO definition was being used as a parameter or just a point of comparison. Is a large value of your perturbation index, I, highly correlated with the occurrence of an SSW defined by the WMO? Some comments about this would be welcome. 

2. Figure 3 can use some clarification. First of all, I didn't see the amount of variance in the first four principal directions reported anywhere---did I miss it? This seems like relevant information. Second, I found the colors and overlapping curves to be hard to parse. The high- and low-pressure levels are colored quite similarly, and the "fast downward progress of the anomalies" (c. line 176) is not so obvious to me. A heat map might be more clear, with each row corresponding to a pressure level and each column a time sample. That is how I'm used to visualizing downward propagating anomalies, e.g., as in Baldwin & Dunkerton (2001) Fig. 2. Third, it is hard to connect mixtures of these principal directions with a pattern of vertical temperature change. 

3. What is the reason to choose sPCA instead of linear regression (perhaps with regularization to promote sparsity, e.g., LASSO)?  

Technical corrections

Fig. 4: Some material is cut off at the interface between the left and right panels. For example, the vertical axis should have a "PC2" label, whereas the "Jul 2009" axis tick label is cut off. Further, because the PCs are not standard, it was not obvious (at least not to me) which direction to follow the black curves in the right-hand panel. I trust they all move in the same direction (counterclockwise, as suggested by the text)? 

Circa line 175 (time-delay embedding notation): there is some mixing between the subscripts on time (t_1,...,t_N) and the time itself (t=1,...,N-(T-1)). It would be better to stick to one notation for simplicity. 

General Quality:

The research presented in this manuscript contributes to the scientific progress of S2S forecasting by leveraging the impact and understanding the dynamics of sudden-stratospheric warmings (SSWs). The authors present a novel three step procedure that combines existing data-driven machine learning techniques to enable a more extensive assessment of SSW dynamics. Using the gained insight they increase the performance of numerical ensemble forecast for lead times above 25 days. Overall, the data preprocessing, the dynamical analysis, the prediction task as well as the post processing are thoroughly motivated and the authors present strong results with according statistics (Cross-Validation) to support their conclusions. As most methods are described clearly and in-detail, the work appears to be reproducible. I have technical questions, regarding the ML forecast, more specifically the neural network, and minor general concerns about the presentation of the results. Should these specific comments be addressed, I recommend publishing this work after minor revisions.

Specific Comments:

1. ML forecast using a deep neural network (DNN): In general your work impressively outlines, a reliable application of machine learning techniques in research, as you leverage physical knowledge to present a concise learning task to the network. However, for me some questions and concerns remain. First, the MLP forecasting is not reproducible, due to the very limited description of the training parameters, input and output dimensionalities and other specifics. Even though to me this is not necessarily main body material, including the information in the appendix or supplementary material (maybe even code or a trained model) is necessary for reproducibility. My second concern is the lack of statistics for the results of the MLP. DNN results sacrifice reliability due to cherry picking, i.e. training only one network. I suggest, for example retraining the model several times given different initial parameters, i.e. deep ensemble approach, yielding more substantial results. In addition, this procedure provides you with the lacking ensemble information, discussed in line 318-320. Lastly, such ensemble approachs as well as the field of Bayesian Learning, I would reframe the statement circa line 317, where you address the default of point forecast for machine learning algorithms, as it is only partly true. Also, I would suggest adding the according citation that supports your argument in line 318-320. 

2. Post-processing Equation: Overall, the description of calculation procedure as well as detailed equations help to understand and reproduce the results. The improvement I want to suggest, concerns the post-processing used to enhance the numerical ensemble forecast. I think combing existing descriptions with an equation would complete the paragraph.

3. Visualization: While the figures in your work provide strong and straight forward visualisation, especially Fig. 3 can profit from improvements, as well as the discussion of Fig. 5. In terms of Fig. 3, I agree with the Comment (RC1) of Reviewer 1 and have nothing to add.  Regarding, Fig. 5, during the discussion of the results you do not specifically mention which of the three plots you address, which sometimes makes it hard to follow the conclusions. Thus, some of the visual arguments do not become evident right away.  My recommendation is either a more descriptive wording or a more distinct visualisation.

Technical Corrections:

In terms of technical corrections, the preprint would profit from overall larger figures, especially Fig.1 and Fig.3.  Even in case of the current figure size, Fig. 1, 2 (left plot), 3, 4 (right plot) and  Fig. 6 have fairly small tick labels on both x- and y-axis. Furthermore Fig. 1 would greatly improve if plotted with a joint colorbar, that also indicates lowest and largest values (with increased tick-size for all values).

In l. 324 I think the authors wanted ‘machine algorithms’ to say ‘machine learning algorithms’.

Finally, I agree with the technical comments of RC1.