Review of the manuscript: "Acceleration of Tropical Cyclones As a Proxy For Extratropical Interactions: Synoptic-Scale Patterns and Long-Term Trends", by A. Aiyyer and T. Wade

Summary and overall recommendation:

The proposed paper has two main aims: first, characterizing the large-scale flow patterns behind rapid acceleration and deceleration of tropical cyclones outside the deep Tropics; second, revisiting the issue of the variability and trends in tropical cyclone (TC) motion from the perspective of acceleration and deceleration. The paper is written clearly and the exposition of the results is generally easy to follow. There are, however, a few conceptual misunderstandings in the interpretation of the results, in particular about the role of phase-locking and blocking during TC deceleration/acceleration and, more in general, during extratropical transition (ET). Other important issues concern the choice of subsets for the composite analysis and the significance of the trend analysis. Some careful revisions to make the scope and the results of the paper more precise are due before this research paper can be granted publication in Weather and Climate Dynamics.

Main comments:

• The advantages of employing TC acceleration as a metric are not immediately obvious: the authors could consider elaborating on this aspect to make the motivation of this work stand out more clearly and, more in general, to contextualize its relevance for our understanding of ET and of its impacts. From the title, for instance, acceleration is meant to be used as a “proxy” for interactions between TCs and the extratropical circulation, but what is actually gained with respect to a similar analysis performed on, e.g., TC translation speed, by comparing subsets of rapidly moving and stagnating TCs on the 30°N-40°N latitude band? The same critique could be extended to the second part: what is the benefit of using the acceleration framework with respect to the simple translation speed? Wouldn’t it be just a more convoluted way to re-obtain the results of Kossin (2018) and Lanzante (2019), while being still heavily affected by the limited length of the data record?
• The authors should carefully consider their use of the concept of phase-locking, which appears to be different from the one established in the literature by Hoskins et al. (1985) and later employed, among others, by Riboldi et al. (2019) [R19]. In that context, phase-locking (or “phasing”) represented the optimal flow configuration for enhanced and sustained baroclinic growth of an extratropical cyclone and the correspondent amplification of a downstream Rossby wave packet. It occurs when an upper-level positive (potential) vorticity anomaly (i.e., a trough) is located a quarter of wavelength upstream with respect to a low-level positive temperature anomaly, leading to 1) sustained tropospheric ascent (by vorticity and temperature advection) in the region of the cyclone and 2) mutual intensification of the two anomalies via the anomalous flow field induced by the anomalies themselves. Phase-locking is inherently three-dimensional, as it consists of an interplay between features at upper- and lower-levels. There are, however, a few points in the manuscript where a more “two-dimensional” concept of phase-locking is considered and this makes the comparison with previous literature problematic. For instance, lines 229-230, “The phasing of the tropical cyclone and the extratropical wavepacket as led to the formation of a cyclone-anticyclone vortex dipole” (that are, however, one to the north of the other); lines 265-267, “we have viewed this as a phase-lock between the ridge and the tropical cyclone” (this is confusing and conceptually incorrect, as phase-locking occurs at best between an upper-level ridge and a low-level anticyclone during anticyclogenesis), or lines 417-418. Also at lines 426-430 the mechanism that holds dipole blocking stationary is described, rather than the phase-locking dynamics during ET.
• More in general, it seems to me that the outlined results relate only marginally to R19, despite it being probably the closest analogue in the literature. For instance, the DECEL subset by R19 features enhanced downstream flow amplification and atmospheric blocking activity, following a classic ET pathway of rapid TC poleward motion ahead of a stagnating upper-level trough. That subset would then correspond to the rapidly accelerating TCs of the current manuscript; however, the discussion of the results relates R19’s DECEL subset with the subset of rapidly decelerating TCs (lines 225-231, 419-424, 436-439). It is also not always clear whether the analogy is drawn with Fig. 10a or Fig. 10b in R19. Another questionable point is the parallel drawn with Fig. 10 of R19, as no vortex dipole was observed or discussed by R19 (lines 260-265, 419-424; see also the next comment).
• For rapidly decelerating TCs, the authors often say that the TC and the anticyclone become “phased” in a configuration of atmospheric blocking (a dipole block; e.g., lines 409-418). This occurrence does not seem realistic, as the horizontal scale and the dynamical characteristics of the large-scale blocking anticyclone are completely different from the ones of the tropical cyclone, and the latter is “enslaved” to follow the large-scale flow induced by the former. Related to the previous main point 3), R19 described how blocking occurs at the end of the Pacific storm track a few days after ET completion (see their Fig. 3) and did not mention blocking occurring at the same longitude of the transitioning TC, or with the transitioning TC being part of it. A direct impact of the TCs “injecting” low-PV air in the block could occur and therefore inflate the ridge (as speculated in lines 216-217), but this needs to be proved. A simpler interpretation of the composites in Fig. 5 or 7 would involve a pre-existent slow-moving anticyclone, maybe an atmospheric block, that decelerates the north-eastward progression of the TC because of 1) the presence of easterlies on the southern side of the block and 2) (more speculatively) the presence of an “inverse beta-effect”, due to that large-scale anticyclone locally reversing the planetary vorticity gradient and effectively “pushing” the TC away from the anticyclone (cf. the selective absorption mechanism described by Yamazaki and Itoh 2009). The authors should check, using an appropriate diagnostic, whether the presence of blocking follows or precedes TC deceleration and therefore modify their interpretation of the results and the discussion section (e.g., lines 423-430) of the manuscript.
• There is evidence of a poleward trend in jet position and extratropical wave activity due to global warming, but there is also evidence of a poleward trend in TC genesis and track that can compensate this, as the region favorable to sustain TCs expands northward. This is one reason why it is speculated that ET storms reaching Europe will increase in frequency as global warming progresses (e.g., Haarsma, R. 2021, https://doi.org/10.1029/2020GL091483 and references therein). How would the authors comment on that?

Specific comments:

Line 24: even though it may seem reasonable to suppose it, are there references discussing the impact of wind shear on tropical cyclone motion? A possible one might be Jones et al. (2000, https://doi.org/10.1002/qj.49712657008).

Line 36: isn’t also Bieli et al. (2019) a more recent reference to justify this high percentage of transitioning TCs in the North Atlantic?

Lines 37-39: this is the only place in the literature review where TC acceleration is cited, it would also be a good place to motivate why it is worth investigating it (see also main comment 1).

Lines 43-44: the work by R19 is definitely relevant, but another relevant reference not included in the literature review might be the recent work by Brannan and Chagnon (2020, https://doi.org/10.1175/MWR-D-19-0216.1) who also tried to investigate phasing during ET and focused on the North Atlantic.

Line 163: composites are built from TCs between 1980 and 2016 (line 144), but here is said that anomalies are calculated with respect to the 1980-2015 seasonal cycle, as for bootstrapping (line 172). Earlier (line 97) it was said that the considered period for composites would have been 1981-2016. Why these differences?

Lines 166-170: storm-relative ensembles are built using data between 1980 and 2016 (line 144) and are based on data drawn from 196 and 168 unique storms (line 169). From a rapid check on Wikipedia (https://en.wikipedia.org/wiki/Atlantic_hurricane_season), “only” 555 tropical systems occurred over the Atlantic. This means that 196+168=364 tropical systems (65.6%, almost 2 out of 3) would then be either rapidly decelerating or rapidly accelerating storms. Aren’t these numbers very high? This percentage seems far from the top and bottom 10% that should be selected to build the composites. Does this total need to be split between curvature and tangential acceleration? Please explain.

Lines 171-174: As the same TC can sit in the 30-40°N latitudinal band for several, consecutive 6-hourly time steps (lines 148-149), the composites are likely built by averaging together consecutive time steps with very similar large-scale flow configuration. For instance, 196 (168) accelerating (decelerating) TCs correspond to 352 time steps in each subset, so each TCs contributes to the composites with 1.8 (2.1) consecutive time steps (~12 hours). This effect of serial correlation needs to be accounted for during bootstrapping, otherwise this might lead to a significance test that is too “easy” to pass. Instead of drawing 352 random time steps, an appropriate combination of dates should be selected so that a substantial fraction consists of couplets of consecutive 6-hourly time steps.

Line 172: are TCs in the period of study selected only between July and October? If this is not the case, then why is the bootstrapping performed only by sampling dates in these months? A more appropriate sampling should take into account the climatological distributions of composite elements by selecting a random date in a time interval centered around the time of each rapid acceleration/deceleration and by attributing it to a random year, as done, e.g., in R19.

Lines 211-217: it would be great if the points discussed in this paragraph were also backed up by some more quantitative analysis. Besides showing in the composites the strengthening jet streak (e.g., with zonal wind anomalies), no metric of downstream impact is employed in the study and it is not clear whether the two subsets have significantly different downstream impact on the flow evolution. The meridional flow index (Archambault et al. 2013), the eddy kinetic energy framework (Quinting and Jones 2016) or Rossby wave packet amplitude (R19) can be possible choices.

Lines 232-253: the composites for strong curvature deceleration are very similar to the ones of tangential acceleration. How would the results change by considering positive and negative values of curvature acceleration according to the local concavity of the track? If the circle associated with the radius of curvature is to the right (left) of the track, a positive (negative) value can be given to curvature acceleration. Would it make sense? Furthermore, the upper and lower decile of curvature acceleration are remarkably similar (line 168, 48 and 32km/hr day^-1) despite the large variability in the size of the curvature circles of Figure 1 and 32km/hr day^-1 is the same value of the upper decile of tangential acceleration: maybe it is worth double-checking if the values written in the manuscript are correct.

Lines 246-257: the wrapping of the anticyclonic anomaly around the TC during recurvature has not (to my knowledge) been discussed in previous literature. Couldn’t the significantly weaker ridge be due simply to blurring of the composite with increasing lead time? It would be helpful if the authors could elaborate on this aspect a bit more.

Lines 351-353: This approach to trend estimation is likely affected by the presence of serial correlation in the data. Was the independence of the acceleration values for each quantile verified? How would the results change if trends of quantiles were computed for each year?

Lines 387-395: the interpretation of the trends would suggest that the interaction TCs- midlatitude storm track is occurring less often. How does this result relate with trends in the occurrence of ET, in this or other studies?

Lines 405-406: what is precisely meant in this context by “the impact of the phasing”? See also major point 2.

Lines 440-445: this paragraph is rather general, how exactly do the results of this study highlight/confirm the presence of bifurcation points during ET? The authors could consider removing this paragraph, as the Discussion part is already rather long.

Lines 445-458: parts of this paragraph are a repetition of the results in Section 6-7 and could be merged with them. This would emphasize the real topic of this discussion paragraph, the question “Is rapid tangential acceleration a sign of imminent extratropical transition?” The following lines provide additional data, but do not give a clear answer to this question, that is left (unsatisfactorily) pending. A more direct answer about whether it is possible to employ acceleration as a proxy of ET could be helpful and might be emphasized in the paper (see also major point 1).

Lines 469-470: the problem of “strength vs frequency” is very important for the interpretation of the results of the second, trend-related part of the manuscript. Without guidance on this aspect, the relevance of the outlined results is difficult to evaluate. The authors can provide some (at least partial) answers to this issue using the data in their possess and I encourage them to try to do so. Trends in strength can be evaluated by considering the strongest/weakest acceleration in each season, trends in frequency by checking the number of TCs underdoing ET in each season or in the number of rapidly decelerating/accelerating TCs (τ<0.1, τ>0.9). The authors might likely have additional, better ideas.

Technical/style suggestions

Line 25: the AMS Glossary of Meteorology refers to “storm track” rather than “stormtrack” (https://glossary.ametsoc.org/wiki/Storm_track), please choose the more usual formulation (unless you have a strong argument to use “stormtrack”).

Lines 51-52: the sentence “While we begin…” can be omitted at this stage.

Line 62: “to” natural factors, but “natural factors” is actually not very precise. Maybe just “attributed these discrete changes to regional climate variability as well…”

Lines 75-76: what do the authors mean with “still” classified as tropical? Does it just mean that each storm must be classified as “TS” at least once in their life cycle to be considered?

Lines 92-93: just to be clear, only the time steps labeled as ET are omitted, right?

Line 130: this “3-day threshold” was not introduced early.

Lines 134-141: As many relevant data are in Table 1, Fig. 1 is not directly referenced in the discussion. Please consider to reference it, or omit it otherwise.

Lines 166-170: this paragraph can be merged with the bullet point ending on line 155, as it is its natural continuation.

Line 210: what is the characteristic signal of a cold front?

Lines 211-217: in which sense a poleward moving tropical cyclone may “either interact with an existing wave packet or […] perturb the extratropical flow”? The two options are not mutually exclusive. In terms of initiation of Rossby waves by TCs, Riboldi et al. (2018) is likely a relevant reference.

Line 261 – PV was already introduced earlier.

Line 278: sections 6 and 7 should be moved, in my opinion, in the rather short section 4 to characterize the evolution of tangential and curvature acceleration during ET. This would help introduce the acceleration framework for the rest of the study.

Line 309: Theil-Sen

Lines 459-467: this paragraph seems a repetition of the results in the previous section, rather than a discussion item. It could be removed or merged with the description of the results in the previous section, or drastically shortened and attached to the following discussion paragraph.

Bibliography

Archambault, H. M., L. F. Bosart, D. Keyser, and J. M. Cordeira, 2013: A climatological analysis of the extratropical flow response to recurving western North Pacific tropical cyclones. Mon. Wea. Rev., 141, 2325–2346, https://doi.org/10.1175/MWR-D-12-00257.1.

Bieli, M., Camargo, S. J., Sobel, A. H., Evans, J. L., and Hall, T.: A Global Climatology of Extratropical Transition. Part I: Characteristics across Basins, Journal of Climate, 32, 3557–3582, https://doi.org/10.1175/JCLI-D-17-0518.1, 2019.

Haarsma, R. (2021). European windstorm risk of post Tropical Cyclones and the impact of climate change. Geophys. Res. Lett., 48, e2020GL091483. https://doi.org/10.1029/2020GL091483

Jones, S.C. (2000), The evolution of vortices in vertical shear. II: Large‐scale asymmetries. Q.J.R. Meteorol. Soc., 126: 3137-3159. https://doi.org/10.1002/qj.49712657008

Kossin, J. P.: A global slowdown of tropical-cyclone translation speed, nature, 558, 104–107,  https://doi.org/10.1038/s41586-018-0158-3, 2018.

Lanzante, J. R.: Uncertainties in tropical-cyclone translation speed, nature, 570, E6–E15, https://doi.org/10.1038/s41586-019-1223-2, 2019.

Quinting, J. F., and S. C. Jones, 2016: On the impact of tropical cyclones on Rossby wave packets: A climatological perspective. Mon. Wea. Rev., 144, 2021–2048, https://doi.org/10.1175/MWR-D-14-00298.1.

Riboldi, J., M. Röthlisberger, and C. M. Grams, 2018: Rossby wave initiation by recurving tropical cyclones in the western North Pacific. Mon. Wea. Rev., 146, 1283–1301, https://doi.org/10.1175/MWR-D-17-0219.1.

Riboldi, J., Grams, C. M., Riemer, M., & Archambault, H. M. (2019). A Phase Locking Perspective on Rossby Wave Amplification and Atmospheric Blocking Downstream of Recurving Western North Pacific Tropical Cyclones, Monthly Weather Review, 147(2), 567-589.

Yamazaki, A., and Itoh, H. (2009), Selective absorption mechanism for the maintenance of blocking, Geophys. Res. Lett., 36, L05803, doi:10.1029/2008GL036770.

Summary and overall assessment:

In this study, IBTrACS and ERA-Interim data on NATL tropical cyclones from 1966-2019 are used to investigate the synoptic-scale patterns that are associated with different characteristics of TC acceleration. Three major synoptic-scale patterns are identified: Rapid tangential acceleration of TCs occurs in cases with a developing extratropical wave packet, resembling a development typically observed during ET. Rapid curvature acceleration of a TC is linked to a dominant anticyclone east of the TC, initiating its recurvature. For rapid tangential deceleration and small (near-zero) curvature acceleration, the synoptic pattern resembles a cyclone-anticyclone dipole. Further, a statistical assessment on the characteristics of TC acceleration and speed is conducted, using quantile regression approach. The statistical analysis reveals that the extremes in tangential acceleration (both rapid acceleration and deceleration), the maximum of curvature acceleration, as well as the translation speed of TCs have decreased somewhat (negative trend) over the past five decades. The most robust negative trend has been found for a 20-50°N band during August and September.

This manuscript focuses on the characteristics on TC motion/acceleration during the interaction of a TC with the midlatitude flow in the NATL. It thus could help to complement the findings from previous work, which put a focus on the characteristics of the midlatitude flow and its wave packets during the interaction. In this context, the manuscript compares the results of this study with the findings of Riboldi et al., who focused their investigation on the translation speed of the upstream trough. Overall, the manuscript is well organized and written in a clear manner, and fits well into the scope of WCD, as it investigates both the dynamics perspective of the interaction as well as climatological aspects. However, the comparison to the results in the context of the work by Riboldi et al. is, in its current version, not fully convincing to me (see major comment 1). Furthermore, some parts could benefit from some more clarity in the description/discussion, and in other parts, information on the approach that has been used is lacking. Once these comments has been addressed during the revision of the paper, it will make a very suitable contribution to WCD.  

Major comments:

1. The discussion of the results in the context of the study by Riboldi et al (2019) needs revision. First, from the discussion in paragraph 258-267, it is not clear whether the reference is made to the ACCEL or DECEL scenario of Riboldi et al., this information (reference to DECEL) is only made in the Discussion (l.421). On the one hand, it sounds reasonable that the deceleration of a trough, during phase-locking, also manifests in a deceleration of the TC. However, I am not fully convinced yet by the reasoning and figures that are presented in this manuscript. The DECEL scenario of Riboldi et al. is conducive to baroclinic interaction and leads to a (strong) amplification of the downstream wave pattern (TC acts as a “wave maker”, Keller et al. 2019). For such a synoptic configuration, I´d expect to see a stronger upstream trough in Fig. 7f-j directly upstream of the TC, as e.g. in Fig. 10 a, c, e of Riboldi et al. Further, when comparing Figs. 4 f-j and 7 f-j with the DECEL scenario in Fig. 10 of Riboldi et al., the position of the TC with respect to the ridge appears to be different. While in the DECEL scenario, the TC becomes positioned in the western part of the ridge during the development, ahead of the upstream trough, where it supports ridge amplification. In Figs. 4 and 7, the TC rather appears to be placed south to the center of the ridge. From the figures provided, its contribution to ridge building is not directly obvious. Please expand on the discussion of these findings in the context of the work by Riboldi et al. This could e.g. include a tracking of the upstream trough to demonstrate the phase locked configuration, additional analysis of the PV (or eddy kinetic energy budget) to analyse the contribution of the TC to the amplification of the ridge, or another suitable means.

2. I am a bit confused by the explanation of the rapid curvature acceleration marking the point of the recurvature of a TC. The explanation in ll. 234-241, on the one hand, sounds reasonable to me. On the other hand, it appears that the (composite) TC in the case of rapid tangential acceleration also undergoes recurvature, as it is e.g. obvious from Fig. 5, but also from Figs. 4 compared to Fig. 7. Please further expand on the differences between the cases of rapid tangential acceleration and strong curvature acceleration to make this point on recurvature clearer. In this context, it could also be of help to see the individual tracks of the TCs included in the composite (e.g. plotting the tracks of all cyclones in the composite after the shift of the grids has been performed).
3. ll. 218-224: Please add information on how the ridge of the extratropical wave packet has been tracked. It would also be good to add information on why the track of the ridge has been used here, instead of the upstream trough, which wraps around the TC, pointing also to a merging of the TC with the extratropical wave packet.

Minor comments:

l. 94-96: The statement on improved reliability of TC data during the satellite era is partly a repetition of paragraph ll.64-70. Consider revising.

l.140-141: Could you add a statement on what this implies?

l.160: Centroid position of *all* storms?

l.168: Given the distribution of curvature acceleration in Fig. 2, the 32 km/h per day as the “near-zero” curvature acceleration seems a bit high. Should this be 3 or 2, instead of 32?

l.170: For completeness, please also state how many unique storms fall into the category of rapid and slow curvature acceleration.

ll.177-181: This information is already contained in the figure caption (same applies to l 200-202). Consider revising.

l.199 and later: The use of the word „system“ to refer to the synoptic structure was a bit confusing to me, as system is typically also used to refer to e.g. a tropical cyclone. Consider revising throughout the manuscript

l.210: Consider adding also information on day +2, as it is included in Fig. 4.

l.211: The downstream trough has not been discussed before. Consider mentioning to already during the discussion of the wave packet in the paragraph above.

l.213: From the figures presented, the strengthening of the geopotential gradient north of the storm is rather hard to detect (a tightening of the geopotential height isobars can somehow be identified in both the left and the right panels).

ll.215-216: Downstream dispersion of energy may occur in both cases (if the TC interacts with an existing wave packet, as well as if it excites a new one)

l.239: Consider adding a bit more information on the study/findings of Aiyyer (2015) here.

l.307: The “all storms” in Fig. 10 are shown in pink/magenta, but text and figure caption state grey.

l.309 and others: Thiel-Sen should read Theil-Sen

l.309: According to figure caption, it should read 20-50°N band.

l.320: This section could benefit with a brief introductory sentence on its aim (even if it is just a sub-section), as e.g. the start into sections 6, 7 and 8, or like the sentences in L. 329-331. Consider adding.

l.325: bottom row -> There is just one row in Figure 12

l.325-327: The shifts in the CDFs for curvature acceleration are there, but not as clear as for the tangential acceleration, e.g. for 0-20N the 1988-1997 period appears to be characterized by more rapid acceleration that the prior and later period.

l.326: Consider adding “not shown” already after the sentence on the CDF over the entire year.

l.327: Could you comment on what might cause this increase in shifts seen in the CDFs, when October and November are omitted. October typically shows the highest percentage of TCs undergoing ET in NATL, e.g. Hart and Evans 2001.

l.360: Could you comment on why the restriction has been made to August-September here, instead of e.g. September-October (same reason as above).

l.362: I do not understand the reference to Table 1 (tau=.5) here. Do you refer to the 0.68 median tangential acceleration in Table 1 for “Full basin”? Please clarify.

l.382: I am a bit confused by the statement that the OLS estimate of the trend is nearly the same value as it was for the annual-mean speeds. From Table 5, the OLS trend for the entire Atlantic and all months is -0.01, but from Table 2, for full basin and all storms, we get a trend of 0.029 (LR) and 0.028 (MK-TS), but maybe I am comparing the wrong information. Consider adding a more specific comparison (e.g. number) for clarity.

ll.405-408: Please be more specific here on how the impact of phasing is evident in the rapid curvature acceleration (as you did above for the rapid tangential acceleration). The aspect of phasing is not discussed in the section 5.2.2.

l.409: “for rapid tangential deceleration and near-zero curvature acceleration”, as there is no curvature deceleration. Same applies to l.421 (rapidly decelerating TCs) and other instances. Consider revising throughout the manuscript.

ll.476-477: For the negative trend in in translation speed and in curvature acceleration this statement sounds convincing, as well as for the negative trend in rapid tangential acceleration. However, could it also serve as an explanation for the observed decrease in rapid tangential deceleration?

l.481: three (?) broad sets of synoptic-scale patterns

Figures & Tables:

Fig. 11 and 12: Labels are hard to read, consider enhancing their size.

Tab. 4: The OLS 95% confidence bounds are put in brackets here, but not so in Tab. 3 and 5. Consider harmonizing.

Typos:

11 T->t

48 shown->show

169: There is a bracket missing.

250: There is a superfluous space in the bracket for Fig. 7.

258: 8a->8b

259: …poleward, the(?) tropical

Several instances: To my knowledge, it is more common to use “storm track” instead of “stormtrack”