General comments: This is my first time reviewing the paper. The paper addresses (from a diagnostic standpoint) an important and relevant question in stratosphere-troposphere coupling regarding the varied downward impact of SSWs, using the framework of weather regimes around the onset time of the SSW. This is a novel approach, and the results would have potential implications for subseasonal forecasters and decision makers. It has great potential.
I have spent some time considering the revisions already undertaken, and the comments of the other two reviewers on the first version of the manuscript alongside the authors’ responses. I commend the authors for their efforts, particularly in terms of constructing statistical arguments for their results with such a small sample size. However, I am unconvinced that the paper fully discusses its results in the context of other diagnostics of stratosphere-troposphere coupling, and it occasionally lacks clarity in its methods or reasoning. I would argue that using the day 0 regime remains a key issue, as I outline below. I believe that once the authors address these points, the paper will be very useful and serve as a good starting point for further studies using this framework.
My recommendation is major revision.
Major comments:
Classification by day 0 regime: A significant sticking point of this study, raised by previous reviews, is the use of the day 0 classification as a basis. Figure 1 and Table 1 shows there are cases when the day 0 regime is different to the dominant regime in the 10 days leading up to the SSW (e.g. 1980-02-29 classified as “no regime” but right up to onset was in EuBL). I would argue that using day 0 is the main door by which this paper opens itself to criticism. There is no physical reason to just pick day 0, especially seeing as there is no persistence criterion on the regime assignment which, by inspection of Figure 1, shows occasional jumps between regimes (i.e. day 0 could be in a different regime to both day -1 and day +1). Indeed, it is only required that the regime is “active” for 6-hours, which seems a concerningly small time period. These aspects could cause confusion in a real-world forecast scenario, something I can see this paper being used for. In most cases, the day 0 regime is largely similar to the modal regime in the 10 days before the U10-60 reversal. The authors must also consider that the reversal of the 10 hPa 60N U-wind is a quasi-arbitrary threshold and the “sudden stratospheric deceleration” or the 65N reversal often occurs slightly earlier (e.g. the 2 January 2019 SSW) so limiting to one day is problematic. A sub-seasonal forecaster will not yet know the exact date of the U reversal, but will have knowledge of the current/dominant regime state. I therefore strongly suggest the authors consider revising the analysis to use the dominant (i.e. modal) regime in the 10 days before, or the 5 days either side, of the U reversal, or address this issue in some other way.
L236 and elsewhere: There needs to be more discussion (at the very least) on whether the different tropospheric responses are due to different stratospheric properties in each of the categories. This section of the text introduces the idea, motivated by the previous reviewers, but not adequately. I am concerned that the results overall are just suggesting – in a new way – that split SSWs or longer-lasting SSWs have different tropospheric precursors and are of higher impact than displacements, which is not new. 4 out of the 6 EuBL events are splits, so it is not surprising these have a stronger signal (I am presuming the classification comes from Karpechko et al. 2017 Table 1 [this should be clarified]). The cold anomalies associated with EuBL also recall the results of Lehtonen and Karpechko 2016 JGR. https://doi.org/10.1002/2015JD023860
L137 The periods 60 days before and after may overlap with another SSW. The separation criterion for an SSW is not stated in the methods either (L85) but this timescale implies 60 days. I think this only affects one example, the SSWs in February and March 2010 which are only around 45 days apart. Karpechko et al. 2017 (QRJMS) did not include the March 2010 SSW in their diagnosis of downward impacts. I would suggest the March 2010 SSW is removed.
L155 Blocking in the more general NAE sector (including Scandinavia/Urals) has been suggested in various studies (e.g. Kolstad and Charlton-Perez 2011 https://doi.org/10.1007/s00382-010-0919-7), not just Atlantic ridge (even the cited Martius paper suggests this). So, I am not sure the authors can argue anything particular about the Atlantic ridge.
Figure 2: the caption states “note the different y-axis in (a)”, but the y-axis in (a) is no different to the others; I would recommend it to be shrunk to better show the variability (presumably this was intended and something went wrong?). The bold lines are also very difficult to discern versus those which are not – could the non-significant parts be dashed, and the bold lines increased in width?
Figure 3: if this paper seeks to be as significant and impactful as it aims to be – which I think it can be – then I strongly think this figure should be for the hemispheric-wide anomalies to allow greater intercomparison with other studies of coupling and a greater potential understanding of NAM behaviour. There is little difference with the Fig A3 as the authors state on L195, so I would strongly encourage swapping 3 and A3 with a continued emphasis that the NAE sector dominates (not surprising given the NAO-AO relationship). Additionally, I think the caption for this figure has the hatching and stippling backwards – should it not be “Stippling (hatching) indicates…overlap by less than 25% (10%).”?
Figure 4: is any significance testing performed? The caption does not state it, nor is any stippling shown. What base period are the anomalies computed from, 1979-2019? Daily? Moreover, have the authors considered detrending 2m temperature to remove the strong warming signal, especially at higher latitudes?
Minor comments:
L26 (and intro generally): there needs to be greater clarity between the NAO defined as an EOF and the regime-based NAO for readers less familiar with regimes.
L34: A further relevant reference would be Matthias and Kretschmer, 2020 MWR https://doi.org/10.1175/MWR-D-19-0339.1
L38 The use of “deterministic” always strikes me as being a bit ambiguous; whether "deterministic" lead-times are the same in the stratosphere (because the timescales are longer). I would suggest being more quantitative. 15 days?
L40 The opening sentence of this paragraph essentially repeats what is said earlier in the introduction.
L50 “..indicators of THE downward impact OF SSW events.”
L61 No need for “often”, i.e. “the stratosphere is ONLY one possible forcing”
L68 “in the NAE region CAN HELP US to understand”
L82 The phrase “is used for all figures”. I would suggest replacing “figures” with “analysis”.
L83 There needs to be some additional specifics on the dataset. Is it used at native 0.75 degree resolution, 6-hourly? Is the reversal required to be daily-mean? This also links with Figure 1 – the y-axis labels have _00 on them; if this is not meaningful, it should be removed.
L83 November to March is not midwinter, it is extended winter. Additionally, by including March, final warmings are potentially included (e.g. March 2016) yet this is not listed. The authors should specify how final warmings have been excluded (e.g. Butler and Gerber 2018 https://journals.ametsoc.org/doi/10.1175/JCLI-D-17-0648.1)
L86 The definition of a regime as a “quasi-stationary large scale flow pattern” has already been included, so this is superfluous.
L87 Why are the seven year-round regimes used, since this study is based in wintertime? This should be addressed. What if the classic 4 Cassou regimes were used? Has this been considered?
L88 insert “tropospheric flow conditions IN THE NORTH ATLANTIC at their onset”
L105 Minor quibble, but I found the readability of the abbreviations to be difficult. Greenland Blocking does not have blocking in its acronym. The authors may wish to consider renaming it to GBL, though I leave this up to them. GL looks like Greenland Low, given than the other blocking patterns have BL.
L110 This is phrased too much like a result. I understand the purpose of the sentences here and it links well with my earlier comment on EOF NAO vs. regimes needing more clarity. The authors should consider rephrasing “they are supressed after a weakening of the polar vortex”, seeing as this behaviour is what the paper is trying to identify.
L114 I would argue SSWs are “RELATIVELY rare” as one every 2 winters is much more common than some phenomena. There is also no need to repeat the number of SSWs in ERA-Interim here as it is stated in the methods.
L115 What does “robust” mean in this context in addition to significant? It is ambiguous.
L182 Why is the response deemed “missing”?
L243 To avoid repeating the word anomalies, “composites of anomalies in 2m temperature and 500 hPa geopotential height”.
L295 The phrasing “stratospheric nudging” is not really appropriate given this is not a results of a nudging experiment.
L299 Word order “…the weather regimes considered here”
Figure A2: the y-axis is not different to the others as the caption states. |
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