I have read the revised version of Mathey et al’s manuscript as well as their response to the comments raised by the reviewers related to the previous version. All references to lines and pages refer to the version including the track changes.
A) The authors responded at length to the main concern related to the quality of the computed focal mechanisms (FM) raised by reviewer #1 and myself. I can follow their arguments partly, however, I am still not entirely convinced of the value and the reliability of the FMs calculated for magnitudes <2.5. This is mainly because it largely contradicts my daily experience in earthquake analysis in the Alps, in which reliable mechanisms for magnitudes <=2.5, even with comparable dense (or even denser) networks, are rather exceptional. If possible at all, it requires extremely careful manual review during picking as well as the FM computation.
I am quite surprised to read that, according to the author’s response, only four of their entire 2200 FMs (about 50% have Ml <2.0) have more than two possible solutions. Again, this completely contradicts my own experience, maybe this is a misunderstanding of what I had in mind. In my own HASH implementation, I use the following parameters, which proved to result in very realistic uncertainties:
dang = 2.0 ! minimum grid spacing (degrees)
maxout = 500 ! max number of acceptable mechanisms output
cangle = 30.0 ! mechanisms are "close" if less than this angle apart (degrees)
prob_max = 0.1 ! probability threshold (cut-off) for multiples (e.g., 0.1)
Maybe the authors use less strict parameters (especially for cangle) or allow for a less broad solution space? Again, in my experience the majority of mechanism result in multiple-solution families for M<2.0 events. The authors also argue that calculating FMs for such small events is mainly possible because of the extremely dense network. However, the network used in their study shown in Fig. 1 is not “extremely” dense on average in my opinion. Unfortunately, no km scale is provided in this map (as in most others), but in many regions the average spacing looks more like 30-50 km to me (which I would not call extremely dense nowadays). In addition, some stations (I guess the lines) are from temporary experiments. One more aspect: Since the authors report the average of all acceptable solutions of HASH, I am wondering if this averaging might lead to a systematic bias towards strike-slip mechanisms in case of extremely poorly constrained solutions. I apologize if this appears extremely pedantic, but my point here is to avoid that readers less experienced with FM calculations get overly confident when using this FM-catalog in future studies. The quality classification currently used seems not sufficient to me to really distinguish between reliable and not reliable solutions and I would have preferred to simply use e.g. the variation in the “acceptable” solutions returned by HASH as a quality measure rather than the predefined classes based on gap etc. Depending on the type of mechanism, the source depth and the distribution of polarities on the stereonet, such parameters can be completely underestimating the true uncertainty of the FM. Using HASH parameters as listed above, in comparison with some manual revised reference-solutions, should have provided better and more robust quality classifications as the one currently used. Nevertheless, I admit that the overall results look reasonable and consistent with previous studies and maybe the FM qualities impact the overall results less than expected. Therefore, as practical solutions to make the quality classification of the presented FMs more transparent for readers I suggest to:
1) Provide a table in the supplement with all the HASH inversion parameters used by the authors to make the results reproducible.
2) As nowadays commonly required in many journals, provide the full dataset used to calculate the mechanisms e.g. in a data repository. The authors disapproved that suggestion according to their response because data seem to be used for another unpublished study. But providing only FM-basic information like Stationcode, polarity, polarity-quality, azimuth-angle, take-off-angle and basic hypocenter information (OriginTime, LAT, LON, Depth, Mag) should be sufficient (no information on phase picks is required if that is still used for something else). With this basic FM-data provided, everybody could use her/his own tools to assess the corresponding FM quality. I strongly encourage the authors to make that basic FM-data available alongside with their publication.
3) With HASH parameters similar to the ones listed above generate a figure which shows: a) number of “accepted” FM solutions (all strike-dip-rake combinations which fit the data within their uncertainties, which means allowing for at least 1-2 outliers, HASH parameter) vs. magnitude for each event. b) similarly, plot number of solution-families (make sure cangle, prob_max are reasonable) vs. magnitude for each event. I would expect that the number of solutions & solution-families reduce for larger magnitudes. Such figure would provide additional information on the confidence of the FM solutions of low magnitude events.
B) While reading the manuscript a second time, I realized that section 3 (which seems the result section) extends over 14 pages (of 35 total). It seems to contain already a lot of interpretation and discussion and all the details listed in this section make it difficult to not lose focus. I would suggest to consider shortening this part to the essential findings. In addition, there are still issues with the English, some sentences are rather awkward or unclear. I listed some examples below, but I definitely recommend another iteration of thorough proofreading by the authors.
C) Final comment: Isn’t the fact that extension in the southern part appears to have no corresponding uplift signal in the geodetic data related to the depth of this extensional zone? In profile 4 extension seems >15 km, isn’t this why no geodetic signal is seen at the surface? Therefore, the comparison of geodetic data and (surface-projected) seismotectonic results and derived conclusions in Fig 11 might be of limited value? Maybe a better comparison would have been (as proposed in my previous comments) to make a stress-regime map limited to FMs in the upper crust (e.g. <10 km) and compare that to the geodetic data?
In addition to these general comments, I have specific ones listed below.
Detail comments:
- Line 19: “down to low magnitudes” -> rephrase. Give exact numbers instead
- Line 24: “since 1989” -> indicate entire period of this study: 1989-2013
- Line 33: “Compression is robustly…” -> Maybe: “Robust indications for compression are only observed at the boundary between the Adriatic and…”
- In many places: be sure it’s correct: “short-wavelength” vs “short wavelength”
- L. 79 (caption Fig 1): -> “… can be clearly identified in the seismicity”
- L. 88: “stress oriented inversion” -> “stress inversion”
- L. 130: Why not simpler: “The preferred solution corresponds to the average solution of all possible acceptable solutions…”
- L. 131: “The HASH code…”
- L. 134: The statement on the Ml computation does not make sense in this location. Move it somewhere to line 185 where you talk about magnitudes. In addition, the statement still seems wrong, it’s not the maximum S-wave, it’s the maximum of P or S wave, right?
- L. 136: “Over the 2215” -> “From the 2215…”
- L. 163: “… on the focal plane solution is lost”
- Figure 2: The axes-annotations/labels are not readable in a,b,c. Make them bigger!
- L. 220: The MATSI software is based on the method of Hardebeck and Michael 2006, no? In the MATSI paper, Vavrycuk 2014 is not mentioned at all. Please check this…
Figure 3: The axes-annotations/labels of the Kaverina-diagrams are not readable at all. Make them bigger! Also, the dots themselves are too small…
- L. 309: what do you mean with “time/energy relation”? You mean moment rate?
Figure 4: Caption: Explain what symbol delta refers to, I assume its dip?
- L. 357: “Lest” -> “Least”
- L. 381: Here you could also compare the results to others studies with similar results
- L. 409/10: Isn’t it “projected to” the surface?
- L. 432: NW or NE Switzerland? Don’t you mean NE?
- L. 443: consistent with… or according to… ?
- Figure 8: Isn’t the higher variation in P expected in a transtensional regime (where P and B are flipping while T remains the same)?
- Several places: “in the overall” -> “in general”
- L. 486: Do you mean “consistent with the surface-projected results”?
- L. 508: “narrow band of strike-slip deformation along…”
- L. 529: “surrounded by a … regime, especially...”
- L. 537: … by a slightly increasing… -> rephrase! By how much?
- L. 540: “geological structures” what do you mean? Lithologies? Tectonic units? specify
- L. 543: “artefacts” -> caused by what?
- L. 558: “of all mechanisms resulting from the projection to the surface”?
- L. 560: “exemplified” -> “documented”
- L. 576: “does not appear to be controlled by the geometry of the former European slab. Both extensive…” COMMENT: I still don’t really understand what the authors mean here with the “former European slab”? All I see in this figure is the geometry of the Moho. And why “former”? isn’t this still European crust/lithosphere? Rephrase this statement! Same later around line 581.
- Figure 10 + caption. In the caption you should describe how the beachballs are projected (they are cut and projected right?) Mention the meaning of the colors of the mechanisms. Since the authors plot all of them, not much detail can be seen
- L. 602: repetition…
- L. 639: -> “… extension previously proposed (CITATIONS).”
- L. 660: I have to admit that I still don’t really understand how such “gravitational collapse” causes N-S directed compression in the Ivrea mantle. Try to rephrase this statement.
- L. 679: “collocate” -> “correlate”?
- L. 681: As the authors mention earlier, the extension in the south is much deeper (profile 4). Isn’t this the reason why the signal in the geodetic data (at surface) is missing? Where the authors see correlation (S-Valais), the seismotectonic extension is shallow…
- L. 699 and elsewhere: Try to avoid the use of “Indeed,”
- L. 703: “When the continuation…” This sentence should be rephrased, bit confusing. Maybe what the authors mean: “…, while the debated continuation … is likely deeper than about 60 km.”?
- L. 715: “can’t” -> “cannot”
- L. 720: Still I don’t fully understand what the authors mean with “purely plate-related geodynamic model” vs their “role of plate motion”. Isn’t everything plate-tectonic related? The authors should improve this part of the discussion.
- Figure 12 caption: -> “… block diagram”
- L. 743: “resolution without the use of a priori … zonation”? |
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