Betreff:
Geophysical Journal International - GJI-07-0290
Von:
sh@ras.org.uk
Datum:
Tue, 21 Aug 2007 03:39:29 -0400 (EDT)
An:
igel@geophysik.uni-muenchen.de

Dear Prof. Igel

We have now received reviews of your manuscript GJI-07-0290 entitled "Source related variations of strong ground motions in 3D: application to the Newport-Inglewood Fault, Los Angeles Basin".  These are appended, together with any additional comments from the editor.  Taking these reviews into account, the Editor, Dr. M. Cocco, feels that major revision of your manuscript is required, after which he will be pleased to give further consideration to publication in Geophysical Journal International.

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Editor: 1
Comments to the Author:
Dear Authors,

I received the reports of two referees who reviewed your manuscript submitted for publication to GJI. Referee 1 asks for major revisions. Referee 2 suggests only minor revisions, but his/her comments involve quite relevant issues; they seem to me more appropriate for moderate or major revisions. I read the manuscript and I also believe that this is an interesting study. However, my opinion is that it needs of major revisions before to be accepted for publication on GJI.

The main problem is the choice of the original contribution of this study. The authors claim that they introduce the concept of numerical Green?s function. As both referees pointed out, this is not true and this idea is not original. The authors present several tests to point out the variability of predicted ground motions (as a function of the hypocenter or asperity locations). This problem is well known in the engineering seismology community and it is one of the motivations for probabilistic hazard assessment. I strongly encourage the authors to clearly define the major and original, or innovative, contributions of this study and to emphasize them in the text.

I suggest to add the source-to-receiver geometry as a third feature characterizing ground motion waveforms (you correctly mentioned at p.2 mid paragraph the crustal structure and the rupture history). 

I also suggest avoiding the use of ?characteristic earthquake? (p.2 bottom) for evaluating ground motion scenarios. I think this is misleading. I suggest to use ?target earthquake? or ?scenario earthquake?.

The authors state at p.3 (top) that the computational limitations motivate the use of ground motion predictions in homogeneous media or for single source scenarios. A similar idea comes out also from the discussion at the beginning of the introduction section. I think that the main reason for computing and predicting ground motion time histories in simplified or homogeneous media is the necessity to account for the variability of source parameters and rupture history. The slip distribution, the location of the hypocenter (earthquake nucleation), the rupture velocity and the rupture propagation are unpredictable and they cannot be constrained by past earthquakes on the same fault. This is the main lesson emerging from the Parkfield 2004 earthquake. For this reason, seismologists are forced to use a huge number of source models to predict ground motions and to assess the variability of selected parameters (PGA, PGV, PGD, etc?). In order to face this computationally expensive task, one choice is to simplify the crustal structure. 
On the contrary, deterministic scenarios in complex 3D media are computed by a simplified source model and complex propagation paths. I totally agree that the simulation of the complete wave field is a major task and I agree on the motivations of the present study. I wish only to emphasize that some of the choices of other studies focused on ground motion predictions are not only due to limited computational capabilities.

I strongly encourage the authors to improve the manuscript in order to make it more clear and accessible to readers. I also recommend to clearly presenting and discussing the real original contributions of this study. Please, include a rebuttal letter explaining all the modifications to the text when you will resubmit the revised manuscript.

Yours Sincerely

Massimo Cocco


Reviewer: 1
Comments to the Author(s)
The idea of Green?s function databank is useful but (as the author himself says) it is not completely new. The paper cannot claim the main objective as ?introducing the concept of NGF?, but rather ?developing the concept?, or so? I think that one way how to increase value of the paper in this respect would be to discuss more the technical details, such as memory requirements, limitations (e.g for different sizes of the studied area, different magnitudes), etc. Try to discuss whether it would be feasible to store the Gip,q functions in order to later convolve them with different moment tensors. Discuss the possibility to use a non-constant rupture velocity. Discuss plausibility of the assumption of the slip rate constant over the fault. 

Strong feature of the paper is employment of the sophisticated 3D finite-difference code, but too little is discussed about its accuracy, frequency limitations, memory and computer time aspects. Please extend the corresponding part. It also closely relates to the above request to describe the technical limitations of the method as regards speed and memory. 

Description of the results is lengthy and makes impression that this paper is only a numerical example, or exercise. Perhaps it was intended as such (?? the aim is to show functionality of the method ??), but the GJI paper needs more. It would profit from a new physical finding. I accept that discussing effects of the hypocenter position or basin edge may be innovative, but it needs some better focus. For example: People tried to explain some specific station anomalies but failed since their model did not properly included both the complex fault and 3D propagation effects; we can explain those data better. Or: Empirical relations from past earthquake failed to explain the observed severe motions during an earthquake in a basin, but this paper can explain such a case. Of course this is rather suggestion for a future work and here, without comparison with real case (except the empirical relations), it is hard to do more. Anyway, perhaps try to better focus your discussion of the results, make it a bit more interesting. Or, simply ignore this comment and keep it in mind for future. Later select a real case with measurements, or, if staying without data and simulate a future event, try to make a hazard assessment and compare with an independent method. I am not requesting it for the present paper, of course.

What is definitely below the GJI level is the writing style. I tried to do many comments just in the manuscript (please find a file with my annotation of your text). The first author should carefully reduce all redundant (?too wordy?) parts of the text, while, at the same time, to extend discussion of missing points (e.g. details about the FD method). He should be also more cautious about such details as units, coordinate axes (e.g. x, y missing in Fig.3). The English language would also need a thorough revision (I feel it although I am not a native speaker). 

I found no clearly wrong points or big mistakes, so I greatly encourage the first author to work a bit more mainly on the presentation of his results.       



Reviewer: 2
Comments to the Author(s)
I think that the manuscript can be published after minor revision and a proper response to the criticism, questions and comments.

The authors should be clear and explicit about the frequency range in which the presented approach can be expected as an acceptable approximation. The statements should appear in abstract and conclusions.

slip speed should be slip velocity (p. 2)

The authors claim that they ?introduce concept of the numerical Green?s function?. I cannot give examples of the papers except that by Graves and Wald (2001), but the statement sounds surprising to me. I would say that the concept has been very clear for years. I admit that this might be just my feeling. Anyway, the authors should exactly say what is really different from the concept of Graves and Wald. In any case I would soften the strong claim of introducing something which sounds, in analogy to the empirical Green?s functions, so logical and obvious.

The authors refer to the paper by Gottschammer and Olsen (2001) as a paper representative of the high-order staggered-grid finite-difference approach. This is really strange given the knowledge of Heiner Igel. The paper numerically compares accuracy of two alternative choices in the imaging method for planar free surface. The problem is that the applied spatial sampling is simply insufficient. Consequently, the paper compares ?accuracy? of two inaccurate simulations. The true meaning of the papers is something like this: two alternative choices give comparably inaccurate results if the spatial sampling is, in fact, insufficient. Unfortunately, there is no other value of the cited paper. I would be very much surprised if particularly Heiner Igel would refer to such paper. I suppose that this irrelevant reference was introduced by some of his co-authors who do not really follow computational seismology. At the same time I hope that the simulations were not performed with 5 grid points per minimum wavelength... 

I think that the empirical Green?s function method was introduced independently by Irikura (1986) and Joyner & Boore (1986). The paper by Irikura should be included in the references if the authors pick up papers from 1986 until 2005.

The statement on the definition of Green?s function by Aki & Richards on p. 5 is not correct. The numerical value of G_ip is just equal to the numerical value of displacement if the amplitude of the unidirectional source impulse is equal to 1 Ns.

Equation 3.18 in Aki & Richards is different from eq. 1 in the manuscript. The reference should be corrected. 

The time dependence of Green?s function in eq. 1 is incorrect.

The sentence ?Assume that sigma_n is small enough and the difference between the individual ... can be neglected? on p. 5 probably should sound ?Assume that sigma_n is small enough and the variations of ... within sigma_n can be neglected?.

The first sentence on p. 6 should speak about Green?s function derivative. Constant G.f. would give zero derivative.

I do not understand the intermediate step, eq. 3, between eqs. 2 and 4. Why is it useful or necessary?

?hollow circles? does not sound good. ?circles? are fine. (p. 7)

Why do the authors use their ME and ignore a better and easy-to-obtain measure of the misfit published by Kristekova et al. (2006)? Is there really any good reason for this?

?The y-component is used for this verification ...? is said on p. 8. Fig. 2 shows the x-component. Is this correct?

Why does the accuracy increase with rupture velocity? (p. 9)

?We truncate the seismic velocities at 1.4 km/s.? This is relatively high value. The authors should comment on an effect of the truncation.

?shear-modulus? on p. 10 should be ?shear modulus?

How do the authors define and determine the threshold frequency? (p. 13)

?explained with? on p. 14 should be ?explained by?

The authors could comment on neglecting interaction between the dynamically rupturing fault and a heterogeneous surrounding medium if they propose a simplified method based on kinematic modeling.

?cycles? should be ?circles? in legends to figures 1, 6 and 9

?equation (3)? in fig. 2 legend should be ?equation (6)?

?hypocentre H1 and H2? in fig. 4 legend should be ?hypocentres H1 and H2?

?asterisk, the epicentre.? in fig. 5 legend should be ?asterisk the epicentre.?

?hypocentre H1 and H2? in fig. 7 legend should be ?hypocentres H1 and H2?

?asterisk? in fig. 7 legend should be ?asterisks?

?in the bottom? in fig. 7 legend should be ?at the bottom?

