Rheology of the Zagros Lithosphere from Post-Seismic Deformation of the 2017 Mw7.3 Kermanshah, Iraq, Earthquake
Round 1
Reviewer 1 Report
I believe that this submission is an improved version of the initial and the authors took care of all the comments I had previously provided.
Therefore, I recommend that the manuscript merits publication.
Author Response
Dear reviewer,
Thank you for your valuable suggestions. We appreciate them very much!
Thank you for your recommendation to our manuscript!
Best regards.
Reviewer 2 Report
Review result for the manuscript by Lv and others, submitted to Remote Sensing:
"Rheology of the Zagros lithosphere from post-seismic deformation of the 2017 Mw7.3 Kermanshah, Iraq, earthquake"
The authors used 2018-2020 Sentinel-1 InSAR time-series data to study the postseismic deformation processes following the 2017 Kermanshah, Iraq, earthquake. The novelty may be in their analysis of time period 2. In this period, they interpreted that the postseismic deformation was basically due to viscoelastic relaxation in the lower crust and the upper mantle, and estimated the viscosity of those layers. The estimated viscosity in the lower crust was in the range of typical values, whereas that in the upper mantle was also in the range of typical values but belong to a group of relatively large values. From this, the authors conclude that the upper mantle is cold and dry.
[General comments]
The manuscript was well written and was easy to understand, although it seems better to give more detailed description on some parts (essence of previous studies for example, to better claim the originality of this research). The authors made an extensive research into previous literatures and compiled a set of studies of postseismic deformation, which is valuable (supplementary material). The novelty of this study may lie in the InSAR time-series analysis, namely, getting the detailed spatio-temporal displacement field in the postseismic period, and in the interpretation of it assuming viscoelastic relaxation (the afterslip also pointed out by them has already been reported by a number of studies). My major concern is that the degree of data fit in the viscoelastic relaxation modeling is poor and is not convincing. In particular the pattern from the ascending direction is not at all explained (the pattern from the descending direction is not well explained too) (Figure 4). What I think out of this is that the principal postseismic deformation mechanism in Periodd 2 is not the viscoelastic relaxation (at least in the horizontally layered structure as the authors assumed). I was surprised, in particular, that the authors did not seem to have considered deep afterslip as the principal mechanism. If the deep afterslip is considered, the whole structure of the paper may change.
[Specific comments]
Line 105: This is a minor comment, but italic usually means scalar. Please respect the notation rule for vector and matrix (gothic etc). Maybe there is a journal guideline for that.
Line 129: Although the authors did not try to correct for the deformation caused by the Aug 2018 Mw 6.0 aftershock (the reason was that the fault parameters cannot be constrained), it should be possible to assess whether the deformation from that earthquake is detected or not, because the authors should have computed a number of interferograms that includes the timing of that aftershock and because the detailed displacement time-series are obtained (coseismic deformation is instantaneous whereas afterslip decays with time).
Line 135: The authors write "For aftershock sequence 1, the best-fitting dislocation has ...". It sounds strange, because the best-fitting dislocation is supposed to correspond to one single earthquake faulting and not to a sequence of earthquakes.
Line 141- (Section 5.2. Afterslip): The authors only used cumulative displacements (time period 1) for the afterslip modeling, even though the authors derived detailed time-series of displacements showing a nice decay pattern. In the current form, there is not much new findings given because previous studies have already pointed out the shallow afterslip. If the authors make use of the time-series data to estimate the temporal evolution of the afterslip, that would provide a new insight.
Line 150: Please indicate the period of the displacements shown in Figure 3.
Line 172 (Figure 4b): There is an unnatural color discontinuity in the Ascending data (around center-bottom). What is this discontinuity?
Linet 172 (Figure 4): As stated also in the general comments, the ascending data in the Time period 2 is not at all explained. I would like the authors to consider about other deformation mechanisms, but at least the reason of this large residual should be mentioned.
Line 176: Section number 5.4 should be 5.3.
Line 222: "previous studies earthquakes" Perhaps remove "earthquakes"?
Author Response
Response to Reviewer 2:
Generate comments:
Comment 1:
The manuscript was well written and was easy to understand, although it seems better to give more detailed description on some parts (essence of previous studies for example, to better claim the originality of this research). The authors made an extensive research into previous literatures and compiled a set of studies of postseismic deformation, which is valuable (supplementary material). The novelty of this study may lie in the InSAR time-series analysis, namely, getting the detailed spatio-temporal displacement field in the postseismic period, and in the interpretation of it assuming viscoelastic relaxation (the afterslip also pointed out by them has already been reported by a number of studies).
Response:
Thank you for your valuable suggestion. Our study is original for two reasons.First, previous studies analyzed shorter time periods and were not able to explore viscoelastic relaxation. Second,in contrast to previous studies we remove the contribution of aftershocks from the post-seismic deformation field. That aftershock deformation is removed is already said among others in the abstract.
Modification to manuscript:
We now say at the beginning of the conclusion (line 284): “We obtained the post-seismic displacement field of the Kermanshah earthquake for the November 2017 to February 2020 time period, longer than previous studies (4 months for Barnhart et al. 2018; 7 months for Yang et al. 2019) ...”
Comment 2:
My major concern is that the degree of data fit in the viscoelastic relaxation modeling is poor and is not convincing. In particular the pattern from the ascending direction is not at all explained (the pattern from the descending direction is not well explained too) (Figure 4).
Response:
Thank you for your comment. We agree that the model fit to the ascending data is not as good as we would like. This is a concern. We have modified the manuscript to acknowledge the misfit, and to offer a possible explanation in terms of tropospheric variability. In addition, we say more clearly that our interpretation in terms of viscosity is based on the assumption that visco-elastic relaxation is the only mechanism producing surface deformation during time period 2.
Modification to manuscript:
We now say (line 188): “This discrepancy can be attributed to the larger tropospheric noise for the ascending data which are acquired during the day when the tropospheric variability is high (local acquisition time of 15:00 and 3:00 for ascending and descending data, respectively).”
We acknowledge the assumption in the conclusions (line 294): “Assuming that this is the only process causing surface displacements, we find a best-fitting viscosity ...”
Comment 3:
What I think out of this is that the principal postseismic deformation mechanism in Period 2 is not the viscoelastic relaxation (at least in the horizontally layered structure as the authors assumed). I was surprised, in particular, that the authors did not seem to have considered deep afterslip as the principal mechanism. If the deep afterslip is considered, the whole structure of the paper may change.
Response:
Thank you for this very valuable suggestion. We agree that afterslip at the downdip fault extension is a potential process that could cause deformation. We have tested this hypothesis and concluded that surface displacement can’t be caused by afterslip. We address this at several locations in the manuscript and provide models in the supplementary material (Fig S2, Fig S3, Table S3).
Modification to manuscript:
We now say in section 5.4 (line 197): “We also explored afterslip models and concluded that they can be ruled out. The fault plane of the best-fitting model locates a few km above the coseismic rupture in the phanerozoic cover (Fig. S2. S3; Table S3), which is geologically not plausible. Besides, the best-fitting viscoelastic relaxation model is characterized by a significantly better rms (rms=√(∑n i=1 residual 2 i)/n) than the best-fitting afterslip model (0.015m versus 0.025m) . We also can rule out afterslip on the co-seismic rupture or its downdip extension because of even higher rms.”
In addition we say in the conclusion (line 294): “Assuming that this is the only process causing surface displacements, we find a best-fitting viscosity of...”
Specific comments:
Comment 1:
Line 105: This is a minor comment, but italic usually means scalar. Please respect the notation rule for vector and matrix. Maybe there is a journal guideline for that.
Response:
Thank you for this very valuable suggestion. We modified this error in manuscript.
Modification to manuscript:
We now rewrite the equation (Line 107): “x2=(dobs-dsim)C-1”(dobs-dsim)-1"
Comment 2:
Line 129:Although the authors did not try to correct for the deformation caused by the Aug 2018 Mw 6.0 aftershock (the reason was that the fault parameters cannot be constrained), it should be possible to assess whether the deformation from that earthquake is detected or not, because the authors should have computed a number of interferograms that includes the timing of that aftershock and because the detailed displacement time-series are obtained (coseismic deformation is instantaneous whereas afterslip decays with time).
Response:
Thank you for this very valuable suggestion. We didn’t try to correct for the deformation caused by the Aug 2018 Mw 6.0 aftershock because we find there is no clear signal associated with it in ascending and descending data. We address this in the manuscript and provide coseismic deformation field in the supplementary material (Fig. S1).
Modification to manuscript:
We now say (line 135): “We don’t consider the 25 Aug 2018 aftershock located east of the epicenter because there is no clear signal associated with it in ascending and descending data (Fig. S1) and no geodetic focal mechanism can be estimated.”
Comment 3:
Line 135: The authors write "For aftershock sequence 1, the best-fitting dislocation has ...". It sounds strange, because the best-fitting dislocation is supposed to correspond to one single earthquake faulting and not to a sequence of earthquakes.
Response:
Thank you for this very valuable suggestion. We address this in the manuscript by adding the sentence that we consider both aftershock sequences as composite events.
Modification to manuscript:
We now say (line 133): “We consider both aftershock sequences as composite events and we obtain elastic dislocation models for aftershock sequences 1 and 2...”
Comment 4:
Line 141- (Section 5.2. Afterslip): The authors only used cumulative displacements (time period 1) for the afterslip modeling, even though the authors derived detailed time-series of displacements showing a nice decay pattern. In the current form, there is not much new findings given because previous studies have already pointed out the shallow afterslip. If the authors make use of the time-series data to estimate the temporal evolution of the afterslip, that would provide a new insight.
Response:
Thank you for this very valuable suggestion. We agree that it is an interesting aspect to investigate the temporal evolution of the afterslip. However, the afterslip period is not the main focus of the paper. We include it because it would not be possible to discuss visco-elastic relaxation in period 2 without discussing afterslip in period 1. Furthermore, it is comforting that previous models hold after removal of aftershock displacement. Thus, we didn’t try to explore the temporal evolution of the afterslip in this paper.
Comment 5:
Line 150: Please indicate the period of the displacements show in Figure 3.
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in Figure 3 caption (line 156): “Uniform slip inversion result of aftershock sequence 1, aftershock sequence 2 for ascending data and descending data. a): aftershock sequence 1, ascending data of 10 Jan 2018 to 16 Jan 2018, descending data of 5 Jan 2018 to 17 Jan 2018; b) aftershock sequence 2, ascending data of 18 Nov 2018 to 30 Nov 2018, descending data of 25 Nov 2018 to 7 Dec 2018; Black solid rectangle…”
Comment 6:
Line 172 (Figure 4b): There is an unnatural color discontinuity in the ascending data (around center-bottom). What is this discontinuity?
Response:
Thank you for this very valuable suggestion. This color discontinuity in the ascending data is caused by the subtraction of coseismic displacement of aftershock sequence 2. Because it is only a small part of the data, we didn’t try to using spatial smooth algorithm to smooth the data in the paper. We add the interpretation about this discontinuity in the manuscript.
Modification to manuscript:
We now say (line 191): “What’s more, the color discontinuity in the ascending data (around center-bottom of Fig 4b-top) is caused by the subtraction of coseismic displacement of aftershock sequence 2.”
Comment 7:
Line 172 (Figure 4): As stated also in the general comments, the ascending data in the Time period 2 in not at all explained. I would like the authors to consider about other deformation mechanisms, but at least the reason of this large residual should be mentioned.
Response:
Thank you for this very valuable suggestion. We agree that the model fit to the ascending data is not as good as we would like. This is a concern. We have modified the manuscript to acknowledge the misfit, and to offer a possible explanation in terms of tropospheric variability. In addition, we say more clearly that our interpretation in terms of viscosity is based on the assumption that visco-elastic relaxation is the only mechanism producing surface deformation during time period 2.
Modification to manuscript:
We now say (line 188): “This discrepancy can be attributed to the larger tropospheric noise for the ascending data which are acquired during the day when the tropospheric variability is high (local acquisition time of 15:00 and 3:00 for ascending and descending data, respectively).”
We acknowledge the assumption in the conclusions (line 294): “Assuming that this is the only process causing surface displacements, we find a best-fitting viscosity...”
Comment 8:
Line 176: Section number 5.4 should be 5.3.
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Comment 9:
Line 222: "previous studies earthquakes" Perhaps remove "earthquakes"?
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say (line 235): “previous studies of earthquakes”
Thanks again for your kind consideration and valuable suggestions!
Reviewer 3 Report
Review of Lv et al., Remote Sensing, 2020
This paper use Sentinel-1 interferograms in ascending and descending tracks to study the first ~2 years of postseismic displacements after the 2017 Iran earthquake. They use a geometry inversion to make uniform rectangular slip models of two aftershock sequences and the afterslip period (6 months) and a viscoelastic model for the viscoelastic period (>2 years). The InSAR processing and the modeling make sense. I think the tables in the supplement are actually an important contribution and provide context for the study presented here.
Major comments:
I would like to see the authors expand a bit more about the InSAR methods and inversion procedure. In particular, is temporal smoothing included in the InSAR TS procedure? How did you decide on priors for the nonlinear sampling problem, and what were they? What covariance matrix is used? Is downsampling performed, and how?
Second, it looks like the Ascending viscoelastic model does not fit the data very well. The overall patterns are not really matched in the model; there is a blue blob that’s not even trying to be fit. If the ascending and descending data are incompatible, it suggests that the viscoelastic model perhaps isn’t a realistic one to be using, so this is concerning. Why could this be? I’d like to see more explanation of the general misfit to the Ascending data, either around Line 188 or in the discussion.
On a smaller note, there’s a sharp phase discontinuity in the Ascending data that’s not visible in the Descending due to the color scale – could it be triggered afterslip, and in what direction? Could it be a topographic feature? It’s a north-south trending discontinuity in the bottom middle of the Ascending data in Figure 4b, and it’s evident in the E-W image as well.
Minor comments:
Line 97: From Table 2, it looks like you invert for strike slip and dip slip as two separate parameters, so you should include that in line 97.
Line 34: crust and lithosphere
Line 91: Did you use global atmospheric models or the phase-elevation ratio? The software can do both, but which did you use?
Line 134: “network inversion filters out” -> “time series inversion filters out” (since NIF is actually a separate thing)
Line 222: previous studies of earthquakes
Line 235: “clay-rich”
Line 281: replace the word “hydrothermal” with something else. Normally we use that term for things like ocean-bottom vent systems.
Author Response
Response to reviewer 3:
Major comments:
Comment 1:
I would like to see the authors expand a bit more about the InSAR methods and inversion procedure. In particular, is temporal smoothing included in the InSAR TS procedure? How did you decide on priors for the nonlinear sampling problem, and what were they? What covariance matrix is used? Is downsampling performed, and how?
Response:
Thank you for your comment. We are using standard analysis approaches from the published literature.We find it more appropriate to refer to those papers than repeating some of their contents. In the following we answer your questions. The clarifications we have done to the manuscript are summarized below.
- Regarding the InSAR timeseries procedure, we didn’t introduce it in detail because the method is not the focus of our the paper. It is explained in detail in Yunjun’s paper (Yunjun et al. Small baseline InSAR time series analysis: Unwrapping error correction and noise reduction[J]. Computers and Geosciences 2019). As explained in this paper, there is no temporal smoothing. We agree that there is a confusion in the literature with some papers using temporal smoothing without acknowledging it (e.g. papers using GIANT software). However, as the Yunjun et al paper is clear we prefer not to address this in our paper.
2a. We are not sure to what you are referring to. Are you referring to the priors for the inversions? For the aftershock sequences, we get the priors about strike slip and dip slip based on the type of earthquakes given by USGS and give a large range for other parameters. For afterslip, we get the priors about strike,dip, strike slip and dip slip based on the coseismic fault property and give a large range for other parameters. The priors are summarized in Table 2. These are standard approaches used by many researchers and we prefer not to talk about this. We agree that it would be nice not to have to select any priors but as you know that does not always work.
2b. Are you referring to the parameters used for quadtree sampling? We use a standard approach as implemented in the GBIS software. We use parameters that just work for us and we test whether we get the same results using different parameters. We agree that this is not optimal and it would be nice to have a more objective, rigorous approach which assures that inversion results don’t depend on sampling. See also point 4 below.
- We used the method used by Bagnardi to calculate the covariance matrix, which is described in detail in: Bagnardi et al., Inversion of Surface Deformation Data for Rapid Estimates of Source Parameters and Uncertainties: A Bayesian Approach,” Geochemistry, Geophysics, Geosystems, 2018,19,2194-2211.
- We use a downsampling method combining uniform and quadtree sampling. We also use uniform downsampling to do the analysis, the results is same as that using combined downsampling method. However, we now only show the uniform downsampling results for time period 2 analysis because our server experienced a power off accident and some data lost which includes results using the combined downsampling method, and we now have no timely access to the computer to redo the calculations. We feel great regret and sorry for it, we mention that the results under uniform downsampling is same as that under combined downsampling in Fig.S5 caption.
Modification to manuscript:
We now clarify how the covariance matrix is calculated (line 110): “We solve the non-linear inversion problem for the elastic dislocations using a Bayesian approach with the Geodetic Bayesian Inversion Software (GBIS) (Bagnardi and Hooper 2018). We also use GBIS to estimate C.”
We now say (line 103):“We sample from the data using a downsampling method combining uniform and quadtree sampling. We use quadtree sampling in the region with significant deformation and in the far field the uniform sampling approach (see supplemental material Fig.S4 and S5)”
We perform the downsampling results in supplement Figure S4 and Figure S5.
Comment 2:
Second, it looks like the Ascending viscoelastic model does not fit the data very well. The overall patterns are not really matched in the model; there is a blue blob that’s not even trying to be fit. If the ascending and descending data are incompatible, it suggests that the viscoelastic model perhaps isn’t a realistic one to be using, so this is concerning. Why could this be? I’d like to see more explanation of the general misfit to the Ascending data, either around Line 188 or in the discussion.
Response:
Thank you for this very valuable suggestion. We agree that the model fit to the ascending data is not as good as we would like. This is a concern. We have modified the manuscript to acknowledge the misfit, and to offer a possible explanation in terms of tropospheric variability. In addition, we say more clearly that our interpretation in terms of viscosity is based on the assumption that visco-elastic relaxation is the only mechanism producing surface deformation during time period 2. We have tested whether afterslip is the potential process that could cause deformation, and concluded that surface displacement’s can’t be caused by afterslip. We address this at several locations in the manuscript and provide models in the supplementary material (Fig S2,S3 and Table S3).
Modification to manuscript:
We now say (line 188): “This discrepancy can be attributed to the larger tropospheric noise for the ascending data which are acquired during the day when the tropospheric variability is high (local acquisition time of 15:00 and 3:00 for ascending and descending data, respectively).”
We now say in (line 197): “We also explored afterslip models and concluded that they can be ruled out. The fault plane of the best-fitting model locates a few km above the coseismic rupture in the phanerozoic cover (Fig. S2; Table S3), which is geologically not plausible.Besides, the best-fitting viscoelastic relaxation model is characterized by a significantly better rms (rms=√(∑n i=1 residual 2 i)/n) than the best-fitting afterslip model (0.015m versus 0.025m) . We also can rule out afterslip on the co-seismic rupture or its downdip extension because of even higher rms.”
In addition we say in the conclusion (line 294): “ Assuming that this is the only process causing surface displacements, we find a best-fitting viscosity of...”
Comment 3:
On a smaller note, there’s a sharp phase discontinuity in the Ascending data that’s not visible in the Descending due to the color scale – could it be triggered afterslip, and in what direction? Could it be a topographic feature? It’s a north-south trending discontinuity in the bottom middle of the Ascending data in Figure 4b, and it’s evident in the E-W image as well.
Response:
Thank you for this very valuable suggestion. This color discontinuity in the ascending data is caused by the subtraction of coseismic displacement of aftershock sequence 2. Because it is only a small part of the data , we didn’t try to using spatial smooth algorithm to smooth the data in the paper. We add the interpretation about this discontinuity in the manuscript.
Modification to manuscript:
We now say in (line 191):“What’s more, the color discontinuity in the ascending data (around center-bottom of Fig 4b-top) is caused by the subtraction of coseismic displacement of aftershock sequence 2.”
Minor comments:
Comment 1:
Line 97: From Table 2, it looks like you invert for strike slip and dip slip as two separate parameters, so you should include that in line 97.
Reponse:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 96):“The model parameters are fault location, length, width, dip angle, strike angle, depth, strike slip and dip slip.”
Comment 2:
Line 34: crust and lithosphere.
Reponse:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 32):“the Zagors lithosphere.”
Comment 3:
Line 91: Did you use global atmospheric models ro the phase-elevation ratio? The software can do both, but which did you use?
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 91):“In this workflow the network of interferograms is inverted for the raw phase time-series and then corrected for the tropospheric delay (we use the ERA5 global atmospheric model)...”
Comment 4:
Line 134:“network inversion filters out” -> “time series inversion filters out” (since NIF is actually a separate thing).
Response:
Thank you for this very valuable suggestion. We use this expression as the referenced paper (Yunjun et al. Small baseline InSAR time series analysis: Unwrapping error correction and noise reduction[J]. Computers and Geosciences. 2019) used (page 11, sentence: “This example, although with an extreme temporal baseline, demonstrates how the network inversion filters out the temporal decorrelation noise”). However, we change this sentence in manuscript in order to eliminate the misunderstandings.
Modification to manuscript:
We now say in (line 138):“They are less noisy than the observed interferograms because the network inversion of interferograms filters out temporal decorrelation noise.”
Comment 5:
Line 222: previous studies of earthquakes
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 235):“previous studies of earthquakes”
Comment 6:
Line 235: “clay-rich”
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 248):“Afterslip is promoted by clay-rich sediments...”
Comment 7:
Line 281: replace the word “hydrothermal” with something else. Normally we use that term for things like ocean-bottom vent systems.
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say in (line 291):“Possible explanations for little afterslip are the thick sedimentary layer, the relatively low heat flow and pore-fluid pressure in the Zagros region.”
Thanks again for your kind consideration and valuable suggestions!
Author Response File: 
Author Response.docx
Round 2
Reviewer 2 Report
My largest concern was that the postseismic deformation field in the Time Period 2 (tp2) was poorly explained and that the afterslip model in this period was not sufficiently considered.
I appreciate that the authors provided results of additional analysis for testing the afterslip model as the deformation mechanism.
I do agree now that the deformation in tp2 is best explained by viscoelastic relaxation, as the authors write in the abstract.
On the other hand, the authors write in the Conclusion that "the post-seismic displacement field is not consistent with afterslip but with viscoelastic relaxation in the lower crust", which I do not entirely agree because a large portion of data is still not well explained. I suggest adding two words in this sentence as "... but MORE CONSISTENT with viscoelastic relaxation in the lower crust".
I still suspect that afterslip (at the same location as tp1) is contributing to the deformation in tp2 (in addition to the viscoelastic relaxation), because the residual patterns for tp2 in Figure 4 somewhat resembles the observed or modeled patterns for tp1, but I do not regard exploration of this possibility is a must. I leave this up to the decision of the authors.
Otherwise, please add "Data", "Model", "Residual" labels in the three columns in Figure S2.
Author Response
Response to Reviewer 2:
My largest concern was that the postseismic deformation field in the Time Period 2 (tp2) was poorly explained and that the afterslip model in this period was not sufficiently considered.
I appreciate that the authors provided results of additional analysis for testing the afterslip model as the deformation mechanism.
I do agree now that the deformation in tp2 is best explained by viscoelastic relaxation, as the authors write in the abstract.
Comment 1:
On the other hand, the authors write in the Conclusion that "the post-seismic displacement field is not consistent with afterslip but with viscoelastic relaxation in the lower crust", which I do not entirely agree because a large portion of data is still not well explained. I suggest adding two words in this sentence as "... but MORE CONSISTENT with viscoelastic relaxation in the lower crust".
Response:
Thank you for this very valuable suggestion. We address this in the manuscript.
Modification to manuscript:
We now say (line 295): “the post-seismic displacement field is not consistent with afterslip but more consistent with viscoelastic relaxation in the lower crust.”
Comment 2:
I still suspect that afterslip (at the same location as tp1) is contributing to the deformation in tp2 (in addition to the viscoelastic relaxation), because the residual patterns for tp2 in Figure 4 somewhat resembles the observed or modeled patterns for tp1, but I do not regard exploration of this possibility is a must. I leave this up to the decision of the authors.
Response:
Thank you for this very valuable suggestion. We agree that afterslip (at the same location as tp1) may continue during the time period 2 and a joint inversion for both afterslip and viscoelastic relaxation is better. However, we decide not to do the analysis of this part because the resolution of our data is not enough to constrain the combined models with both afterslip and viscoelastic relaxation. We add this explanation in the revised manuscript.
Modification to manuscript:
We now say (line 202): “We did not consider combined models with both, afterslip and viscoelastic relaxation, because the data lack the resolution to constrain all model parameters.”
Comment 3:
Otherwise, please add "Data", "Model", "Residual" labels in the three columns in Figure S2.
Response:
Thank you for this very valuable suggestion. We address this in the supplement material.
Modification to supplement material:
we now adding “Data”, “Model”, “Residual” labels in the three columns in Figure S2.
Thanks again for your kind consideration and valuable suggestions!
This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.
Round 1
Reviewer 1 Report
Review comments
Article Number: remotesensing-694477
Post-seismic deformation of the 2017 Mw7.3 Kermanshah earthquake and static Coulomb failure stress change analysis with aftershocks
by Xiaoran Lv, Yun Shao, Falk Amelung, Shu Ye, Ming Liu and Chou Xie
*Overview
In this paper, the authors investigated the 1.5 year post-seismic deformation of the Kermanshah earthquake based on the Sentinel-1 A/B data and the InSAR time series method.
First, two aftershock sequences were investigated and the fault parameters of these aftershocks were obtained using the non-linear geophysical inversion method. Then, by removing the contributions of these aftershocks, the authors revealed that the afterslip along the up-dip extension of the coseismic zone in the first 190 days was the dominant post-seismic mechanism.
The result obtained in this study is convincing me and interesting. However, this paper includes several problems as described below and moderate revisions are needed before publication.
1. The structure of the paper is confusing. For example, the detailed method to calculate the static Coulomb stress changes is described in “Result” chapter. These methods should be described in the “Method” section.
2. English grammar is no excellent and there are typos. I recommend the authors to ask native English speakers to improve the readability.
3. The authors referred many several previous studies investigating the coseismic and postseismic deformation of the Mw7.3 Kermanshah earthquake. One advantage of this paper is the analysis period of a 1.5 year-long post-seismic period, longer than previous study. I agree with this point, but the more discussion on the comparison with previous studies is
necessary. Are the results obtained in this study consistent with those by previous studies, or what is the difference between the results in this study and those from previous studies?
4. How about the assumption of the apparent coefficient of friction? In this study, the authors assumed an apparent coefficient of friction of 0.8. However, the most-frequently-used apparent coefficient of friction is not 0.8 but 0.4 as discussed by King et al. [1994]. Laboratory experiments on frictional slip in rock indicate high values, such as 0.5-0.8 [e.g.,
Byerlee & Brace, 1968]. In contrast, fluid injection would cause high pore-fluid pressure, which would then decrease the apparent coefficient of friction. The robustness of obtained conclusion for the setting of apparent coefficient of friction should be discussed.
5. At the paragraph which explains how to calculate the Coulomb stress changes, I recommend to refer following papers, which calculate the ΔCFF for nodal planes of focal mechanism solutions to reduce the uncertainty of receiver faults in a heterogeneous stress fields where earthquakes with various types of focal mechanism are occurring.
Ishibe, T., K. Satake, S. Sakai, K. Shimazaki, H. Tsuruoka, Y. Yokota, S. Nakagawa, and N. Hirata (2015). Correlation between Coulomb stress imparted by the 2011 Tohoku-Oki earthquake and seismicity rate change in Kanto, Japan, Geophys. J. Int., 201, 112-134, doi: 10.1093/gji/ggv001.
Toda, S. (2008). Coulomb stresses imparted by the 25 March 2007 Mw=6.6 Noto-Hanto, Japan, earthquake explain its ‘butterfly’ distribution of aftershocks and suggest a heightened seismic hazard, Earth Planets Space, 60, 1041-1046.
6. The aftershock sequence on 11 January 2018 seems to be swarm-like activity, which can be attributed to the decrease in fault strength due to the increase of pore-fluid pressures rather than the increase in static Coulomb stress changes. It may be better to describe this aspect.
7. In Lines 132-134, I don’t understand well. The static Coulomb failure stress change can be also calculated reasonably for heterogeneous fault slip models and there are numerous studies which incorporate the heterogeneity of fault slip.
8. In Lines 225 and 230, the authors describe the length and width of best-fitting fault planes, while there are not such a resolution from this analysis. Please consider to round these values.
9. In Figure 4, the inverted fault shown by the black solid rectangle is not consistent with the LOS displacement. The peak uplift is located at the southeast of the rectangle fault. What is the reason for the mismatch between the inverted fault and LOS displacement? Please consider to add the descriptions.
Other minor revisions
1. Figure 1: The date of the 11 Des 2017 Mw5.4 earthquake should be “11 Dec 2017” Please add the explanation on the color bar shown in the right side of the figure (e.g., elevation (m)). “Magitude” should be revised to “Magnitude”. In the figure caption, the authors
described that “The black dashed rectangle marks the coseismic fault” without referring any paper. Please add the reference unless that the coseismic fault model is obtained in this study.
2. Figure 2: I think it’s better to create the map showing the temporal changes of LOS displacement, if possible.
3. Table 1: The depth of upper crust, lower crust and upper mantle should be described as 0-25 km, 25-45 km, and 45- km, respectively, or the “Depth (km)” should be revised as “Top of Depth (km)”.
4. Table 2: There are no needs to show the date of the earthquake (i.e., 20180111 and 20181125.
5. Table 3: Please consider the resolution of fault parameters and round the values if necessary.
Author Response
Dear reviewer,
First of all, we would like to thank you for your constructive comments to improve our manuscript. We have carefully addressed all the review comments and improved the quality of this manuscript accordingly. Please see the attachment.
Author Response File: Author Response.docx
Reviewer 2 Report
This paper reported postseismic deformation following the Kermanshah earthquake in Iran-Iraq border area. Among their conclusions, little contribution of viscoelastic relaxation is solid, and interesting TO ME. However, overall quality of scientific writing as well as English usage is terrible! I believe that Prof. Amerung, a co-author and native English speaker, never checked this manuscript. The contents of all the peer-reviewed paper should be properly conveyed to the readers (NOT TO THE AUTHORS). Also, the authors must explain the importance of this earthquake and originality of their approach clearly (I couldn’t find them). Therefore, I strongly recommend to reject this paper. I raised some points below, but there are numerous strange sentences in the manuscript (I can’t raise them all).
1, Title is not informative. What did they want to say?
2, Terrible English. Also, I can’t find logical connection between the sentences.
For example…
Line 1: Sentinel-1 A/B data and the InSAR time series method (MintPy) was => Were
Line 20: We never say “post-seismic mechanism”.
Line 20-21: “and the fault geometry and uniform slip was” => were. Also, this sentence is redundant.
Line 40: “Viscoelastic relaxation often occurs in the far field” I don’t understand the meaning of “far field”.
Line 47 “deformation 2D time series” I don’t understand what is 2D time series…
Line 48 “GPS, InSAR and terrestrial laser scanning (TLS) are three methods measuring surface displacement.” How about levelling and EDM? I don’t understand author’s purpose.
Line 51: “InSAR is the most promising technique to fill the gaps of geodetic measurements”
What is the gaps? I can’t find any good reason that they think InSAR as the most promising!
Line 54: “the post-seismic [20, 21].” Post-seismic what? The word “seismic” is adjective!!
Line 55: “The Mw 7.3 Kermanshah earthquake occurred on” I can’t find any reason why do they suddenly start talking on this specific earthquake. They are now talking about geodetic tools.
Line 57: strongest => largest
Line 59: “post-seismic of this earthquake.” Post-seismic what?
Line 82: “on third” I don’t understand the meaning.
Line 83: GPS data shows => show
Line 88: “Even though Kermanshah earthquake is located at the collision region between two plates.”
I can’t understand what do they want to say…
Line 174: “4.4 Horizontal and Vertical Deformation Resolve” Strange English.
Line 217-218: “Assumption of one fault with uniform displacement and non-linear geophysical inversion are used.” Terrible English. Just terrible.
Line 235-236: No explanation for (a) to (f) in the caption. Strange.
Line 239-241: No explanation for (a) to (f) in the caption.
Line 247-248: “using a non-linear geophysical inversion using GBIS” Don’t write “using” twice.
Line 311: “lake of viscoelastic relaxation” I can’t understand the meaning.
2, Authors did not explain the importance of this earthquake to wide variety of readers. They also did not explain the originality of their approach clearly.
Line 70 “Here we use Sentinel-1 A/B ascending” Why do they use Sentinel? Why do we need the Sentinel data? Why should we learn about this earthquake?
Line 214-215: “We use ascending and descending coseismic displacement (Figure 4a, 4d; Figure 5a, 5d) extracted from post-seismic displacement time-series” It is impossible to extract coseismic displacement from post-seismic time-series.
Line 296-297: “confirming the results of Barnhart” Then what is original findings (and those importance) of this paper??
3, Lack of citations, etc.
Line 109: SRTM need reference.
Line 107: Authors must insert proper citation for ISCE.
Line 176: “(Wright et al 2004)”. Line-of-sight is a common sense. No need for reference. Also, why do they refer to this paper?
4, All the assumptions should be justified or well explained.
Line 132-134: “we only invert for uniform slip …. Because static Coulomb failure stress change can be calculated reasonably based on uniform slip values”
This is strange reasoning! Even if the Coulomb failure stress change looks good TO THE AUTHORS, uniform slip assumption should never be justified for that reason.
Line 137-138: “In this paper, we use a Maxwell body to describe the rheology of the lower crust and upper mantle.” Why? All the assumption must be accompanied with good reasoning.
Line 172-173: “However, we only calculate and consider static Coulomb failure stress change in this study.” Why?
Line 184-185: Authors should not neglect NS displacement without good reason.
5, More physical explanations are necessary.
Figure 7: Authors must indicate synthetic result of after-slip for time-period 2.
Line 324: “6.3 Uplift/subsidence coseismic ratio modification due to post-seismic rebound”
In this section, the authors just write what they obtained from numerical simulation. The authors must explain the physical mechanisms of coseismic and postseismic deformation and their mutual relationship quantitatively. I don’t understand whether the authors considered gravity effect or not, which could be important for vertical deformation.
Reviewer 3 Report
I would like to thank the authors for their submission to the Remote Sensing journal.
This is a post-seismic study of 2017 events at the borders of Iran-Iraq. The specific sequence attracted the attention of scientific community. The authors here present an enhanced dataset of SAR data to perform time-series. Final goal is to investigate which mechanism between afterslip and viscoelastic relaxation is the dominant one, during the postseismic period.
The study is well-written and potentially publishable. Below are my comments.
Major comments
1 There is a complete absence of the details of the non-linear inversions performed for aftershocks 1 and 2. Were all the parameters constrained during your inversions? The coseismic signal was probably good enough. But what about the other inversions? Was any of the parameters fixed? You could update the already existing table or make a new one for the supplementary. The same for the postseismic signal that you used for the afterslip modelling. Was the post-seismic signal good enough for all the parameters to be constrained? Was anything fixed?
2 There are no uncertainties presented for the fault parameters. Add the uncertainties for all the estimated parameters that you present. And also describe how you estimated them.
3 For the co-seismic inversions (and especially for the Mw5.5 event), did you make any atmospheric corrections to the signal? If yes, how?
4 Since there are already published studies partially overlapping with yours, stress better in the conclusions and in the introduction what is new in your study when compared to the others’ and what are the new findings (e.g. larger data span, uplift-subsidence ratio etc).
5 I agree that a uniform slip is ok for the afterschocks, but for a mainschock with a source of a size of 39.3 km x 17 km, wouldn’t a slip distribution model be more realistic than a uniform slip model? It is up to the readers to decide, since the study focuses mainly on the post-seismic investigation.
Minor comments
-Define what does “Strslip” stands for in Table 3.
-Line 65 . “… and thought that afterslip…”, use a different verb.
-For a better reading flow, you could change a little bit the syntax of the phrases staring in Lines 223 and 228. For example start the phrases informing the reader for which afterschock you refer to at the beginning of the phrase and not at the end.
-Provide a reference for SRTM DEM
-Add Ding et al. 2018 Geophys. J. Int
-It would be nice for the reader to have a few more words about MintPy
-The same for PSGRN/PSCMP. Please add some descriptions on the code used.
-In all the figures that you present the sources, show which is the shallower part of the rectangle (using thicker line? Or by using different colour).
I trust that the authors will take into account the comments and I invite them to provide a revised version of their work.
Author Response
Dear revieser,
First of all, we would like to thank you for your constructive comments to improve our manuscript. We have carefully addressed all the review comments and improved the quality of this manuscript accordingly. Please see the attachment.
Author Response File: Author Response.docx
