Dear Authors
Thank-you again for your revised manuscript. I append below both reviews now received. Unfortunately the more critical original reviewer declined to look at it again. Then I felt it necessary to obtain another opinion. Unfortunately for the progress of the manuscript, this review, the second below, questions (“colourfully” but reasonably, I think) the scientific value of the work. [Of course you do not only consider the radon transform, but the Fourier Transform is not obviously better. I am left to wonder if there is any method that could be reliable unless on speed is dominant in a way that would need to be defined].

These review comments will need addressing if the manuscript is to be published. [Apart from good scientific practice, there is the practical consideration that if or when your manuscript is published all the comments will be available “alongside” and so must be seen to be addressed.]

I am sorry this process is proving lengthy.
Yours sincerely
John Huthnance


Report 1
First, I want to thank the authors for their response to my previous comments. Overall, the authors have suitably addressed my comments and clarified the points I raised. While I still think that this paper is largely an academic exercise, it is scientifically valid (assuming the analysis has been properly done), and so it is not my place to hold this paper up. I have only one remaining important comment and a few minor ones.

The authors dismiss my comment about the arbitrariness of the metric used to assess the accuracy of the various detection methods by saying that “Indeed, our choice is arbitrary but so is any other choice”. The authors’ response is rather unscientific and I disagree with it. Choices about skill metrics should be governed by logical rather than arbitrary considerations and they should be clearly justified, otherwise the results will be suspect. On a related comment, I think that rather than saying whether or not a method detects the true propagation speed based on an arbitrary metric, it would be far more useful to provide a measure of the uncertainty associated with estimates of propagation speed.

The authors write “Indeed, our choice is arbitrary but so is any other choice. We will emphasize it in the revised text.”. However, I cannot see where this has been emphasized in the text. Similarly, the authors write “As for the number of realizations, we didn't find significant difference between 25, 50 or 100 repeats.” This is not mentioned in the paper and I think it should.


Report 2
I rather struggle to see the point of this paper; it seems to be setting up an implausible strawman problem and then shooting it down.

The idea behind the radon transform is that, in situations where there is a dominant propagation speed, it identifies that speed as a direction in t-x space along which the variance of the mean signal is maximised. The emphasis is on "dominant speed". This requires that there be either a single mode propagating at that speed with squared amplitude larger than the sum of the squares of the amplitudes of all other modes, or that there be a cluster of modes with similar speeds sufficient to be dominant over the modes with different speeds. The former case clearly requires the single mode to have a much larger amplitude than all the other modes. That seems to be what this paper is showing (also from Figure 5, we see how the "random" choice of speeds for other modes will tend to produce a clustering of energy at slower speeds: the result will depend on how the randomly chosen modes happen to cluster as a function of theta, with different choices giving different results).

It is hard to think of a physical system for which this extreme case is a plausible model. If there is propagation, there is likely to be a smooth variation of speeds as a function of frequency and wavenumber. The aim with radon transforms as applied to Rossby waves is usually to identify the long Rossby wave speed, which is independent of frequency and wavenumber and hence will apply to a range of modes (and hence a clustering of energy at a particular angle in t-x space), with the shorter waves becoming more dispersive and thus producing a smaller signal in the radon transform. It is arguable whether this is really achieved (see a wide range of papers recently with Dudley Chelton, among others, arguing that the dominant speed tends to be more related to nonlinear, coherent eddies). Even in the purely linear limit, the radon transform clearly isn't the appropriate tool if interest lies in the dispersive part of the wave spectrum. In that case a two-dimensional Fourier method seems a good place to start, together with the idea of searching for a dispersion relation rather than simply a single speed. For example, see Zang and Wunsch (JPO 1999, doi: 10.1175/1520-0485(1999)029<2183:TODRFN>2.0.CO;2).

So there seems to me to be little added value in this contribution. The radon transform remains a good way to identify a dominant speed when there really is one. When there isn't, it is a poor method. There is nothing new or controversial about that.

Dear Authors
Thank-you for your responses and revised manuscript. I am asking now for minor revision because there are a couple of points (below) where I think (re 1) your response needs to be incorporated in the manuscript and (re 2) I think you have not quite “met” a point being made by the additional reviewer. [I remind you of the practical consideration that on publication all the comments will be available “alongside” and so must be seen to be addressed. It is better that the manuscript itself is “self-contained” by effectively addressing the comments – implicitly rather than as directly as in a response.]
Yours sincerely
John Huthnance

1. In your response to “Report 2” you write “The reviewer might be right . . . . However, in the real ocean it is impossible to determine the relevant amplitudes and the number of nodes (N).” This is a good point! [It causes me to retract my clause “. . dominant in a way that would need to be defined”]. I think you should make this point in the discussion. Of course it has implications that one might never be able to have confidence in an estimate of propagation speed – except perhaps by trying various inherently different methods of estimates and so estimating possible uncertainty from the range of results. I think something like this ought also to be in the discussion.

2. In Report 2 “. . or that there be a cluster of modes with similar speeds sufficient to be dominant over the modes with different speeds. . . . . The aim with radon transforms as applied to Rossby waves is usually to identify the long Rossby wave speed, which is independent of frequency and wavenumber and hence will apply to a range of modes (and hence a clustering of energy at a particular angle in t-x space), . . .” I don’t think you really address this. Some more discussion is needed. Preferably I would think some more experiments where the dominance is expected from many modes close to a particular speed rather than one mode with much larger amplitude.

Dear authors
Thank-you for your revised manuscript. I am now accepting it. The next step is therefore for you to enter it in the Ocean Science publication process. It will be copy-edited; I don't expect much change but you should check that your intended meaning is retained.
Thank-you for publishing in Ocean Science.
Yours sincerely
John Huthnance