the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 20 Feb 2024
A new characterization of the North Atlantic eddy-driven jet using 2-dimensional moment analysis
Abstract. We develop a novel technique for characterising the latitude, tilt and intensity of the North Atlantic eddy-driven jet using a feature identification method and two-dimensional moment analysis. Applying this technique to the ERA5 reanalysis, the distribution of daily winter jet latitude is unimodal with a mean of 46° N and a negative skew of -0.07. This is in contrast with the trimodal distribution of the daily Jet Latitude Index (JLI) . We show that our method exhibits less noise than the JLI, casting doubt on the previous interpretations of the trimodal distribution as evidence for regime behaviour of the North Atlantic jet. It also explicitly and straightforwardly handles days where the jet is split. Though climatologically the jet is tilted south-west to north-east, around a fifth of winter days show an opposite tilted jet. Our method is simple, requiring only daily 850 hPa zonal wind data, and diagnoses the jet in a more informative and robust way than previous methods.
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CC1: 'Comment on egusphere-2024-318', Kristian Strommen, 20 Feb 2024
Dear Jacob et al.,
Your new jet latitude methodology is elegant and informative. However, two comments arose when reading:
- The unimodality of phi is presented as evidence that the trimodality exhibited by the JLI may not be genuine. In particular, the authors state that it "[casts] doubt on the previous interpretations of the trimodal distribution as evidence for regime behaviour of the North Atlantic jet" (Abstract). However, in paragraph starting L185, the authors look at the centres of mass of EDJOs (Figure 6) and note that "[t]he spatial distribution of all centres of mass (Figure 6a) shows a trimodal structure", with a southern and northern centre corresponding to split jet days. Thus while phi itself is unimodal, your methodology does seem to detect some form of multimodality. Given the emphasis placed in the Abstract and Conclusions about the trimodality of the JLI, it is surprising that the trimodality of Figure 6 is not commented on further. How do the authors interpret this result? It seems at a glance that it could be interpreted as giving a different 2-state regime view of the jet, with one state being a "basic jet" and the other state being "split jet". This would suggest a more nuanced view to the difference between JLI and phi.
- Negative skew in phi is reported, with more weight in the southern tail of the distribution. How "significant" is this skew? Is it e.g. robust to resampling, or consistent with noise from a Gaussian? In CMIP models and reanalysis, the northern peak of the JLI is quite sharp, but the southern peak often more like a "shoulder". Could the skew be the imprint of a southern jet "shoulder"?
Obviously I'm not an official reviewer, but would be grateful to hear the authors thoughts on these questions nonetheless!
Best wishes, Kristian Strommen
Citation: https://doi.org/10.5194/egusphere-2024-318-CC1 -
RC1: 'Comment on egusphere-2024-318', Clemens Spensberger, 19 Mar 2024
Review of "A new characterization of the North Atlantic eddy-driven jet using 2-dimensional moment analysis" by Jacob Perez et al.
In the manuscript "A new characterization of the North Atlantic eddy-driven jet using 2-dimensional moment analysis" the authors suggest a more robust re-definition of two widely used jet metrics for the North Atlantic, jet latitude and tilt. The motivation, method and results are generally clearly presented, with only some caveats in the comments.
I still cannot recommend the manuscript in its current form for publication. First and foremost, I find it hard to regard their method to be a significant step beyond the current the state-of-the-art. In essence the authors so far only provide a technically more robust definition of jet latitude and tilt, but they do not address the conceptual problems associated with this approach (usage of low-level winds influenced by boundary layer processes, fronts, and orography; usage of low-frequency data to describe synoptic-scale dynamics; their jet latitude is still a zonal mean over a tilted storm track). Interestingly, the authors voice some of the same criticism over their predecessors, but then repeat the criticised choices in their method without further discussion. The resulting method is certainly more robust than its predecessors in a technical sense, it just remains unclear to what extent that constitutes a significant improvement if the main problems are of a conceptual nature. At the same time, conceptually more robust jet definitions would be available (cf. major comments A-C for details and references).
Having said that, I think the suggested method has potential for conceptual improvements beyond the state-of-the-art, but they are unfortunately not utilised so far. For example, the authors replicate existing jet latitude and tilt diagnostics, but do not explore how (combinations of) other moments might yield (more/other/complimentarily) useful diagnostics. May be some of combinations of moments describe jet waviness, waveguideability, or sharpness, in a useful and conceptually novel way? Further, while the authors in principle do allow for several EDJOs per time step, they then discard that additional information for most of their analyses (cf. also major comments C and D).
In summary, I think the authors need to...
(a) become much more precise in their criticism of previous studies given where their method actually can offer an improvement relative to the current state-of-the-art,
(b) properly acknowledge that alternative, conceptually more robust jet definitions would be available, and
(c) offer some conceptual improvement over previous North Atlantic jet metrics... before this manuscript is suitable for publication.
C. Spensberger
Major commentsA) L34-35: I disagree. In my view, the main limiting factor for the reliability and interpretability is the attempt itself to capture daily North Atlantic jet state by a characteristic latitude and tilt based on time-filtered data. Time-filtering obscures physical processes, and trying to capture the widely meandering North Atlantic jet by these two metrics is necessarily an extreme simplification. For applications where such extreme simplification is permissible, simply considering, for example, the latitude of maximum wind might very well be sufficient. Replacing the latitude of maximum winds by a weighted mean latitude does not solve any of the conceptual limitations of this approach.
B) L22-24 versus L55: In the same vein, it seems weird that the authors criticise Woollings et al. (2010) following White et al. (2019), but then themselves use the same low-level winds to define their jet indexes. The jet indices suggested in this manuscript will be equally much affected by the Greenland orography as the jet indices in Woollings et al. (2010), although the orographic influence will likely manifest itself in a different way. More generally than White et al. (2019), Spensberger et al. (2023) recently showed that low-level winds are not a good indicator for the presence of eddy-driven jets. Even just a latitude threshold would be a better choice than the low-level wind for separating subtropical from eddy-driven jets. Spensberger et al. (2023) suggest defining eddy-driven jets as jets occurring below the isentropic level of 335K.
C) Section 2.2/Figure 1: I do not agree that the jet identification method is particularly simple, nor does it seem particularly robust. I am certainly biased here to some extent, but to me the Spensberger et al. (2017) definition of jet axes as "well-defined lines of wind maxima" (using basically one threshold to mathematically define the term "well-defined") even seems conceptually simpler than jet objects iteratively defined by the flow chart in Figure 1. In terms of implementation, Spensberger et al. (2017) is surely somewhat more complex, but then both a reference implementation (Spensberger 2021) and the actual detections for ERA5 (Spensberger 2023) are publicly available. The same is true for JETPAC, a conceptually similar jet definition by Manney et al. (2014) that has been used in a series of studies on jet and storm track dynamics.
Regarding the robustness of the definition, the iterative definition of jet objects (repeating steps 2-4) will make the identified jet objects sensitive to small variations in the input wind field. I have experimented with similar approaches, and specifically the topological property of what is connected above the chosen wind speed threshold is essentially random. A more robust way to segment the wind field into several jet objects would be to use a watershed algorithm, that is iterating through the wind field not by "flooding" based on seed points, but rather iterating through the grid points in order of decreasing wind speed. Then, for every point in isolation, one can use well-defined and explicit criteria to decide whether a grid point is (a) a new jet object, (b) an extension of an existing jet object, or (c) a grid point either merging or separating two jet objects.
As context and illustration for this comment, I would also point out the preprint of Auestad et al. (2024): any spatio-temporal filtering in the jet definition muddies the otherwise clear relation between the jet and latent heating. Only when considering the instantaneous meanders of jets is the latent heat release clearly concentrated on the warm side of the jet, the side where one would physically expect it.
In short: using either the Spensberger et al. (2017) jet axes or the Manney et al. (2014) JETPAC would yield more reliable and interpretable results than the new method proposed here.
D) L186-187: I don't understand that choice. The authors seem to thus discard one of the stated main benefits of their method: the ability to potentially detect several jet objects per time step.
E) There are several large-area figures which do not contain large amounts of information (in particular Figs. 3, 5, 6, 10 and 11; to some degree also Figs. 2 and 4). I am sure some of the information therein could be combined and conveyed in a more compact way. The discussion of some Figures remains quite superficial, indicating that some Figures might more be illustrating side remarks than the core idea that the authors want to convey. Such Figures might with benefit not be shown or moved to a supplement.
Specific/minor comments
L14: Correction: Spensberger et al. (2017) detect both STJs and EDJs. Spensberger et al. (2023) thoroughly investigate how to separate STJs from EDJs, and thus implicitly offer an EDJ-only detection algorithm.
L68-70: How does the flooding handle object mergers? I.e. what happens if two seed points are connected at a level above the minimum wind speed? Does the stronger EDJO always win? If so, there would be more robust ways of separating jet objects (cf. major comment C).
L81-85: This seems to confirm my hunch in L68-70.
L185: Note that these statistics will depend heavily on the filtering of the input field. Without filtering, there'd be several EDJs (and probably also EDJOs) almost all the time during winter.
L204-205: With that finding, it must be the mass-weighted definition of the jet latitude that makes the decisive difference, rather than the option for multiple EDJOs per time step?
Fig 8: Beyond a tilt angle of 20 degrees, neither jet latitude metric seems to do justice to the composite average wind pattern. And the composite will certainly be cleaner than the individual time steps from which it is compiled.
L225-226: I am not able to follow this argument. Which search are the authors referring to, and why would that cause noise/ a lower autocorrelation?
L248-249: As in main point D: curious that the authors chose to move this result featuring a novel aspect of their method in the supplement and focus the main manuscript on replicating known analyses.
L277-288: Given the authors so far only offer a technical improvement, I feel these conclusions are way too strong. Being as bold as the authors, I could equally validly claim that the results of Spensberger et al. (2023) and preprint of Auestad et al. (2024) suggest that also results obtained with the new method introduced here would better be reconsidered using a more robust jet definition such as theirs. I would of course never do that ;-)
References
Auestad, H., Spensberger, C., Marcheggiani, A., Ceppi, P., Spengler, T., and Woollings, T.: Spatio-temporal filtering of jets obscures the reinforcement of baroclinicity by latent heating, EGUsphere [preprint], https://doi.org/10.5194/egusphere-2024-597, 2024.
Manney, G. L., Hegglin, M. I., Daffer, W. H., Schwartz, M. J., Santee, M. L., & Pawson, S. (2014). Climatology of Upper Tropospheric-Lower Stratospheric (UTLS) Jets and Tropopauses in MERRA. Journal of Climate, 27(9), 3248-3271.
Spensberger, C., Li, C., & Spengler, T. (2023). Linking Instantaneous and Climatological Perspectives on Eddy-Driven and Subtropical Jets. Journal of Climate, 36(24), 8525-8537.
Spensberger, C. (2021). Dynlib: A library of diagnostics, feature detection algorithms, plotting and convenience functions for dynamic meteorology (1.1). Zenodo. https://doi.org/10.5281/zenodo.4639624 .
Spensberger, C. (2023).ERA5 jet axes 1979-2022 [Data set]. Norstore. https://doi.org/10.11582/2023.00120 .
Citation: https://doi.org/10.5194/egusphere-2024-318-RC1 -
RC2: 'Comment on egusphere-2024-318', Anonymous Referee #2, 27 Mar 2024
Review of "A new characterization of the North Atlantic eddy-driven jet using 2-dimensional moment analysis" by Jacob Perez et al.
This study presents a new method for characterising variability of the North Atlantic eddy-driven jet on 10-day timescales. The method identifies ‘eddy-driven jet objects’ based on a threshold U850 value, and employs spatial moments of the objects to define jet latitude and tilt diagnostics. This overcomes some well-documented shortcomings with other widely-used jet diagnostics (notably by identifying multiple jet objects when the flow is highly distorted, thereby providing a cleaner interpretation on such days) whilst remaining relatively simple to calculate.
The manuscript and figures are clear and well-written. It is a methods paper which does not contain any new science results as far as I can tell, but the results presented provide an informative, albeit light-touch, comparison to other jet latitude and tilt diagnostics from the literature. I note that RC1 is concerned about whether this new method provides any significant improvements over the previous methods. My view is that this decision can be left to the wider community by the extent to which the new method is adopted. I do, however, have several minor issues with the results as currently presented which I would like to see addressed.
Main Comments
- Given (as noted in CC1) you place strong emphasis on the fact the distribution of phi is unimodal and state that this ‘casts doubt on the previous interpretations of the trimodal distribution as evidence for regime behaviour’, I am also surprised you do not explore further the fact that the spatial distribution of EDJO centre of masses in Fig 6 remains trimodal. Please provide further interpretation of this result (for example, it could be informative to explore how the centre of mass distribution (Fig 6b) varies for days when the JLI is in its N, M or S position), or else describe more clearly how you reach your conclusion regarding the evidence for regime behaviour.
- Given this is a methods paper, I would like to see a more detailed analysis of the robustness of the methodology to the choices made. As some examples, you use 10-day LP filtered winds as input and a threshold of U850*=8m/s. What’s the justification for these choices, and to what extent are the results sensitive to them? The reason I ask is that whilst the 10-day filter is used in the ‘standard’ Woollings et al method, the results obtained there are largely insensitive to this choice. I suspect the EDJO objects, in contrast, may break up into many smaller objects if less or no temporal smoothing was applied.
Minor Comments
L3: Please provide a confidence interval for the skewness to convince the reader it is robustly negative (also in the main text).
L5: What do you mean by ‘less noise’? Please be more specific.
L5: This sentence suggests that the method casts doubt on the stated interpretation because it is less noisy. Is this really what you mean?
L17 (first half): Please provide the specific refs which give this interpretation.
L55: I realize that you use the same domain as Woollings et al deliberately, but it is striking (Figs 2 and 4) that most of your EDJOs are cut-off, particularly at the western boundary. Would you expect greatly different results if your domain extended further west?
L75: What distance is used if the major axis intersects the object boundary several times?
L201: ‘median value’ -> ‘median difference’.
L213: Figure 9 is only mentioned in passing, and can be removed without losing any of the messages of the paper.
L246: To my mind, the fact that the variation is NAO/EA space is smoother for phi and alpha than JLI and JAI is a key result of the paper which should be mentioned in the conclusions (and possibly abstract). However, is it not the case that the total variance is larger for JLI and JAI than phi and alpha (estimated from Fig 7)? Therefore having smaller variance in each quadrant does not, by itself, evidence this point. Please provide a cleaner analysis of the fraction of variance explained.
L264: It would be good to see some analysis of the jet width, which would add a more novel component to your results.
L287: I’d question that the method only has three tuneable parameters (presumably U850*, L* and L_lam*?). Specifically, the choice of low-pass filter and domain of study surely have a big impact of the results.
Fig 2 caption: Which dates are shown?
Fig 10: Please add an indication of sampling uncertainty to the autocorrelation lines to indicate where the differences between the different diagnostics are robust.
Citation: https://doi.org/10.5194/egusphere-2024-318-RC2
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