|Review of 'Fast descent routes from within or near the stratosphere to fEarth's surface in Fukuoka, Japa' by Itoh and Narazaki submitted to Atmospheric Chemistry and Physics.|
This is the review of a revised manuscript. The authors have addressed all the points that I raised in my previous review. Some of them have been adopted and others rejected. I do not know what other reviewers think about it, but the changes that authors have introduced in this new version are minor. They have got some improvements in the manuscript, but they seem unnecessarily combative with most of the ideas pointed out by the reviewers. Moreover they recognize lack of familiarity with the topic of STT exchange. Therefore I recommend taking more carefully the comments by the reviewers and accepting suggestions based on experience.
My recommendation is now 'Minor revision', but I suggest to the Editor that all my comments are taken into account before publication.
About your replies and other major comments:
As to the evaluation of “not too suprising”, at least we were suprised at the following findings:
1. We discovered the mid-latutude route, which could not be expected. Also, the potential temperature sharply decreases along the trajectories of this route.
2. The high-latitude route is so systematic that the time sequence of descent by tropopause folding, southward transport by a strong trough, strong descent at the southern edge of the
trough, and downward transport by appropriate near-surface disturbances is considerably regular for many cases.
3. There is a case (case 19) in which descent is as large as 6892m for two days, with 4659m
recorded on the first day.
==> None of these is surprising to me. Maybe there are not too much existing literature on the topic, but being familiar with it includes a fair knowledge about what is obvious or at least a plausible and expected result. The latitude for FIHE and Boulder is similar. With your method you have found a far amount of trajectories with origin much poleward' but you can not state that mechanisms are completely different in the studies of Wang and Polvani (2011) or Añel et al. (2012). Some differences are that Polvani et al. use a temporal domain of 17 days and Añel et al. (2012) use 10 days (as in your case). But different methods can provide slightly different results and this must be included for a balanced discussion of the topic.
In some way is striking to me the lack of convervation of PV and potential temperature. I think that it could be useful for readers if you include some extra discussion about this in the manuscript. That is, how the work with the data and computations drive to this result. In some way you have alread highlighted it in the current version of your work, therefore probably your feeling is not too different of mine about this.
there is a striking systematic difference between MT events and the tropopause folds in the present study, that is, occurrence frequencies show maxima in midltitude (i.e., zones of maximum cyclogenesis) in the former but in high latitudes in the latter. Pan et al. (2009) attribute MT events to latitudinal migration of the tropical tropopause over the extratropical one. Therefore, MT events may include not only tropopause folds but also other phenomena. In other words, MT events and tropopause folds do not correspond to one-to-one.
==> Fair enough. But then, are you considering foldings as the only way for STE?. Simply this is not true. Foldings are not the only way for stratospheric air reaching surface levels as I have already pointed out. Moreover, they should be really profound foldings and this is a low percentage of the total. Have you checked one-to-one that all your trajectories are related to synoptic-mesoescale systems of latitudinal and vertical dimensions letting such exchange? I do not recall seeing it in the manuscript, therefore if you make a generic statement about the potential causes, you must include a discussion broad enough to support the attribution of causes. Sure, tropical overlapping could disturb your results and drive to MTs in vertical soundings, but these cases are already removed with the analysis of trajectories. The point here is that a hot-spot for MT formation is probably related to a greater percentage of STE, lowering of the tropopause height and more effective mixing between layers. This facilitates STE (with independence of the tracer used) and it is what should be pointed out in the manuscript.
The program that trajectories are pursued was made on our own, because the accuracy is very important in this study and free softwares are sometimes not fully accurate. However, similar trajectories could be traced by using any free softwares.
==> I guess that you have not clear the concept of 'free software'. Please, check http://www.gnu.org/philosophy/free-sw.en.html for a definition. 'Free software' has nothing to do with price and I think that you have not correctly understood it. If you have writen a piece of software (code) to perform the measurement work this is ideal. You should submit it as supplementary information, in this way everybody can check it and it can be included as part of the review process. The Creative Commons license used by ACP is compatible with software licenses and therefore of application.
You also mention the use of the Dennou library. I have not been able of checking its license, but from the Ruby's version I guess that it could be a license from the BSD family. The Dennou library is included in the acknowledgements of other papers and you could do the same here, but I suggest passing it to the methods if you have a reference that you can use to cite and credit the developers.
Other minor points:
- I insist on my suggestion of including 7Be in the title, I think that it is a strong point of the manuscript that will make it interesting for the scientific community and more read. As the authors are worried about the length of the title I suggest to remove 'fast descent routes' from the title. It is a concept hardly quantifiable from three words.
- lines 67-68: this is not true, Chen et al. 2013 study and shows with backtrajectories and the synoptic-scale meteorological situation the mechanisms driving to this phenomenon. A more complete explanation of the feedbacks is provided in a paper recently accepted for publication in the Journal of Atmospheric Sciences (Chen et al. 2016, Reasons for the extremely high-ranging planetary boundary layer over the western Tibetan Plateau in winter, available in Early Online Releases). One of your replies to Reviewer#3 is about the work by Skerlak et al. (2014): you reasoning is that PBL is not equal to surface, but this depends a lot on orography. The works by Chen et al. (2011, 2013 and 2016) show clearly how STE to the PBL can be the almost the same than surface and in fact how the PBL can be considered to overshoot the tropopause. The problem right now in your manuscript is that you cite Chen et al. 2011 that is only a description. Maybe you could use the work of 2013 as I had recommended before. Probably what happened is that you mixed both studies after the study in 2011 was suggested by the Reviewer#1.
Please, have into account this full perspective when preparing a next version of the manuscript.
- line 83: please, remove 'to have only'
- line 174: you state 'This period is sufficient for capturing the statistical characteristics'. Being more correct probably what you mean is that a six years measurement period is a sample of the population enough to assume 'a priori' that the magnitude of the sampling error is acceptable. Therefore I suggest you to remove the sentence or rewrite it in a more accurate way.
- line 274: the last word would be better 'could'
- line 522: '6000 m'
- line 707: the surname in the reference is 'Gimeno'