
Response to referee A:

We thank referee A for their reading of the paper.

We interpret referee A's response as essentially stating that the paper is `very interesting' but it is not written in a way that is suitable for publication in PRL.

We believe that the first section of the paper that discusses the new methods to find stationary black hole solutions is written in a very general manner that is accessible to a general audience. Obviously a good familiarity with GR is assumed (and we think this is totally reasonable), but contrary to the claim of the referee, we do not believe any familiarity  with numerical GR is assumed. We have carefully reviewed the relevant past work on the numerical stationary problem (in the section 'Harmonic Einstein equations'), and then discussed our new approach. Furthermore we have very deliberately done this is a non-technical manner in order to be accessible to non-experts. The referee states that "the
new method is explained in half a page with essentially only words
(with is perhaps adequate for workers in the specific field, but would
probably give most non-experts not much of an idea). " We exactly disagree with this, and believe that a very long and technical discussion would not be appropriate for non-experts. 

The referee also states;
"... a significant part of the text has been
labeled as "supplementary material" (which is longer than the paper
itself!). I think significant parts of the supplementary material are
not just "optional" additional information, but rather results and
explanations without which the main part of the paper would be hard to
read. "

Again we disagree with the referee. We feel the letter is self-contained and it is entirely possible to read the main text without referring to the supplementary material. The reason we include the supplementary material is so that anyone who wishes to reproduce our numerical results, or is concerned about their accuracy, can then access more detail. We expect very few readers would wish to do this, even experts in AdS-CFT. It is our experience with numerical work that other practitioners often want to see 'gory' details of convergence and implementation. Conventionally such details are simply entirely excluded from letters, whereas now the supplementary material gives a vehicle to give these details and help people have confidence in the calculations. We emphasize again that these details are not meant for the lay reader, or indeed experts in AdS-CFT, but rather for people who genuinely wish to reproduce or perform similar calculations. Particularly for numerical or experimental work we feel it is good that there is some way to get more detail about the computations or experimental setup than the classic letter allows - we think this was precisely the intention of PRL in adding the new supplementary material section, and we are trying to use it as such.

Obviously we could just have excluded any supplementary material altogether, and then this discussion would not have arisen, so we hope that we will not be penalized for making use of the supplementary material to provide more detail than in the past would have been possible. The key point is that the main text can be read without reference to the supplementary material, and we feel that this is the case. We note the referee does not point to a particular part of the supplementary material which they feel is essential.

The referee states;
"It may not be easy to present this
rather technical work in 4 pages to a general physics audience; but
that would mean that it would be better to publish it elsewhere."

As stated above, we believe we have discussed the new numerical techniques in a very non-technical and general manner.  However the referee is certainly correct in saying that AdS-CFT is very technical, but we think it is not correct to say as they do that we assume to much familiarity with it. We focus only on the relevant aspects of AdS-CFT, and describe in general terms in the introduction why the problem under consideration is of interest. Whilst letters should be readable to a general audience, we believe it is not the job of a letter to give a pedagogical introduction to all aspects of AdS-CFT in 4 pages, and in addition describe new material - this would clearly be impossible. Rather we believe the purpose of a letter is to explain in general terms why a problem in AdS-CFT might be of general interest (here, since one can describe strongly coupled quantum plasma, which is certainly a problem that in principle is of general interest) and then give details of how progress has been made. 

In order to better address the concerns of referee A, in the first paragraph we have added a review to the fluid/gravity correspondence, and also explicitly pointed the reader to excellent reviews on AdS-CFT and above eqn 2 we have directed the reader to a detailed review on the relevant aspects of numerical relativity, all of which are written for lay readers.

In summary, in this letter we cover a number of areas, describing new methods in numerical relativity, and then their application to an interesting problem in AdS-CFT which also has links with hydrodynamics, quench physics and strongly coupled systems. It is precisely because our methods have future potential to impact diverse areas, and that we also have interesting physical results, that we have submitted our work as a letter. However we acknowledge that in such a case it is very much a matter of opinion as to whether the letter successfully engages the general audience. We believe it does, and referee A obviously feels it does not. 




Response to referee B:

We thank referee B for their careful reading of the paper.

Their main comment is;
"Regarding results on strong quenching, the authors claim to find
superluminal plasma flow. This claim doesn't seem warranted to me, in
that it is purely based on interpreting components of the stress
tensor as if it were an ideal fluid, which by construction is not the
case in the strong quenching regime."

In fact the result that the plasma flow is superluminal is quite independent of the hydrodynamic approximation (ie. interpretation as an ideal fluid). It is the statement that one cannot boost to a rest frame of the vev of the CFT stress tensor. We have reworded the text in the last paragraph of p. 3 and the first paragraph of p. 4 to emphasise this, and better explain what we mean by 'superluminal'. In addition it is simple to show that the superluminality we see directly corresponds to violation of the usual (ie. weak, strong, dominant) energy conditions for the vev of CFT plasma stress tensor. Again we emphasise that this has nothing to do with the hydrodynamic approximation to the plasma behaviour. We thank the referee for making us explain this point more clearly.

Violation of energy conditions in a quantum vev of a stress tensor is certainly possible, but one might reasonably expect pathologies to be associated to a state which does this. AdS-Kerr provides a CFT dual where precisely when the dual vev of the stress tensor is superluminal (and violates the same energy conditions as ours) then the gravity solution is super-radiantly unstable (and argued to be turbulently unstable). This provides some evidence that our state may well exhibit an instability, which in analogy with AdS-Kerr may be turbulent ie. associated to a cascade of energy to short wavelengths. We have tried to word these statements in the paper so that they are not stated as fact, but rather just are our suspicion. Clearly further work analyzing stability would be needed to make any definitive statements.

In response to the minor comments;

* It is mentioned (pg 3, right column) that the method is numerically
stable setting V at -1 and T at +1 ... is there some reason for this?
Were other possibilities tried and found not to be stable?

We certainly tried other possibilities and most did not work. The one we used worked well and gave a stable numerical algorithm. We understand that we must fix two pieces of data to fix the moduli of the solutions, but we unfortunately don't understand why one way gives a numerically stable algorithm and others do not. We have not elaborated on this point precisely because we have nothing useful to say at this time.


* In the text it says Fig. 1 shows x v/(1+v^2), but the figure says v?

Indeed the main text was poorly worded, and we have tried to improve it. The intention in the text was not to imply that it was v/(1+v^2) that was to be plotted. Now we have explicitly stated in the text that v is plotted.


Regarding the supplemental material:

* Have "vv component" in column 2, pg 1 ... should it be "zz
component"?

Many thanks for spotting this - it should be 'tt' and has been amended.


* On the top of page 3, right column, it says we "expect" all x
derivatives to vanish for reference metric ... isn't this metric fixed
and given for all time, so this known?

We have reworded this, as it was evidently misleading. We are saying that we expect the derivatives of the metric functions (T,...,A) should decay exponentially in \rho, and hence have vanishing derivatives in x at the boundaries $x=\pm 1$, for our choice of coordinates (ie. for our choice of reference metric - recall the reference metric determines the coordinates the solution is presented in). I believe the referee took our text to indicate that derivatives of the reference metric were vanishing, which indeed they do, but this was not the intended meaning. We hope the text is now clearer.


* It is strange that second order finite differences would fail. What
exactly goes wrong? The smoothness of a solution is not a-priori
related to the order of convergence, so I don't see why this would be
the reason. Likewise, following eq(16), taking numerical derivatives
of a numerical solution does not in general lower the order of
convergence of the numerical derivative, and hence functions
calculated from it. What is the convergence factor for a metric
function by itself? If (for example) a boundary condition controlling
the "moduli" is only being implemented with first order accuracy, the
convergence of the metric and functions derived from it will only be
first order, even though errors in the Einstein eqns (15) or
divergence of the stress tensor will be higher.


We have simply observed that second order finite differences in our implementation fail, but we don't know why. It could be that a more delicate relaxation process would yield a convergent algorithm. We have had no such problem with fourth order or higher differencing. We are using the usual local stencils, so for second order nearest neighbour, for fourth, next to nearest neighbour, etc. We suspect that the non-locality associated to a wider stencil may be important in controlling smoothness at the horizon, but that is simply a suspicion. So it might be using a second order accurate, but wider stencil, would work well - we haven't tried this.

With regard to decreasing convergence with increasing derivatives, we mean that if one approximates a function at a point with a polynomial of n^th order, using a standard nearest neighbour stencil, then convergence of the difference of the actual m^th derivative to the m^th derivative of the polynomial approximation at that point becomes worse with increasing 'm'. For m>n of course the situation is maximally bad, as the polynomial approximation gives zero as the answer, and so there is no convergence. 







