Report of Referee A -- LQ8404/Varn
In the revision of this Letter, the authors have addressed some of the difficulties of the initial form. The introduction is greatly improved and the statement on the virtues of their approach is much more clearly stated and put in the context of the previous work on the subject. It is still difficult to appreciate the e-machine method without extensive reference to the literature, but that is understandable because of the limited space of a PRL letter. I look forward to seeing the more complete statement in reference , (in preparation). Although I am not entirely convinced that all my previous concerns have been met, I feel that the authors have gone sufficiently far in that direction to make this Letter acceptable, and so I recommend that the revisied version be accepted for publication in PRL as it is.
This manuscript describes a computer algorithm that can be used to interpret x-ray diffraction spectra from closed-packed systems. I find that algorithm, though it may be new, does not offer any new physics in either x-ray diffraction field or in the field of information retrieval.
Furthermore, what the authors have presented are not convincing to show their method actually works, or works better than others. I have serious questions about the validity of their results. If I understand this correctly, there are possibly 3 times 8 parameters (or more) in their algorithm with r=3, as represented in Fig.2 or Fig.4. That is more than 24 parameters! The curves they try to fit, Fig.1 or Fig.3, each contains only 30-40 experimental points! This is not at all convincing.
Finally, I agree with the first referee that PRL may not be the right journal for this work. A more specialized journal such as optical communications would be a better choice, if the authors could substantiate their findings.
My conclusion is that the manuscript should not be published in PRL.
The manuscript describes the calculation of x-ray diffraction patterns or rather of a single 1-D section through reciprocal space for 1-D-disordered crystals. Calculations are compared to 1-D scans of disordered ZnS from the literature.
The authors have previously applied successfully 1-D-statistical mechanics to fundamental problems like the crystalline ground state of matter. In the present manuscript they turn to the interpretation of experimental 1-D disorder scattering.
The most interesting part of this work is certainly the way information on the correlation function is being extracted from the diffraction pattern without having to make a distinction between host-structure and fault. Also, the authors claim that their method produces a unique model with the minimum number of correlations necessary to obtain a given quality of fit, a property that would be most welcome.
While acknowledging the novelty of the approach itself I have, just as the two previous referees, some doubts about the relevance and broad interest to the physics community. In fact I'm not even convinced that the approach is of much relevance (or practical use) to the small subset of `diffractionists' at least in its present, rather 'academic' state.
The authors claim that no knowledge of the structure is required for their evaluation of the disorder, but that is only true if one has a rather narrow view of what a known crystal structure is. In fact, in their example, the complete structure is known except for the stacking sequence along one direction. The whole treatment is valid only under the assumption that the problem is strictly 1-D and that the stacking disorder does not influence the layers themselves or the interlayer distance. These requirements are certainly not met by many systems of practical importance.
I'm not even sure that they strictly apply to ZnS at least as far as the 1-D character of the second sample is concerned which has been heat treated in such a way that the hexagonal stacking sequence has disappeared. The problem is that one hexagonal direction corresponds to four equivalent cubic directions. Is it guaranteed that the resulting intergrowth (or 'twinning'?) does not produce intensity close enough (within the experimental resolution) to the 1-D scans that it could be responsible for some of the features the authors try to explain? After all, are the authors aware of such potential resolution problems? Frankly, this is hard to believe as long as 'borrowed' data is used.
The statement that, in previous approaches, only Bragg-intensities have been taken into account is true only if one confines oneself to the very academic branch of disorder theory.
In other disciplines people (trying to solve real problems) frequently use the information from Bragg-intensities and diffuse scattering together to evaluate average structure and disorder. Examples are, in the case of powder diffraction (x-rays or preferably neutrons), the work of Egami, Billinge, Takagi and several others who use the pair distribution function (PDF) approach to account for (correlated) deviations from an average structure. That approach can, in principle, be used for the whole spectrum of order/disorder from the ominous 'ideal crystal' with no disorder scattering right through amorphous solids like glass or polymers where only local order prevails. Other groups, in the single crystal case, have analysed for many years 3-D diffuse scattering data from correlated point defects (Proffen, Welberry, Neder.) by, for instance, reverse Monte Carlo (RMC) techniques.
Of course these approaches are not at all a-priori as they all start from a more or less well known local or average structure and, upon optimisation, get quite often caught in pseudo-solutions which fit the data very well but have very little to do with reality.
There is, therefore, certainly a need for methods that can evaluate correlations without being based on a model that more or less predetermines the result. Yet, the statement that the authors are the first to use Bragg- and diffuse scattering intensities simultaneously is not correct.
Another field, more closely related to 1-D-stacking defects in ZnS: There is a whole community that tries to better understand (quantitatively) 1-D stacking defects in micas or clay-minerals from their combined Bragg- and diffuse x-ray scattering (from powders). These compounds also span the whole range of disorder from strictly periodic to completely random (s. c. turbostratic) stacking. Moreover, these materials are far from the idealized assumption of the stacking being independent of the structure and stoichiometry of the layers. In fact, they are characterized by a systematic correlation of the type of stacking defect with stoichiometric variations within the layers and in the space between the layers. My impression is that this is the rule rather than the exception in 1-D disordered systems.
This would mean that the practical applications of the method of Varn et al. would be quite limited and P.R.L.'s requirement of broad interest would not be met.
Referee B has risen the question of the number of parameters that have been used (and adjusted) to fit the data. I perfectly go along with his statement that the data presented certainly does not support many parameters. I'm afraid the fact that the algorithm starts from the simplest possible correlation model and advances gradually to more complex models (with much more parameters) does not guarantee that the 'inflation' of the number of parameters is stopped early enough. Almost any spurious peak or shoulder in the 1-D scan will probably be accounted for by a sufficiently complex correlation model. For more complex structures, the simultaneous fit of the data on several lattice rows would most probably be inevitable.
Another point of discussion is the quality of the data, not only possible systematic errors due to scattering into the 1-D-scan from outside this reciprocal lattice row but also the statistical quality. No error bars are shown for the experimental data points in figs. 1 & 3 and, at least after normalization, the reader has little chance to judge on the statistical quality of the data. Are the deviations shown (and the improvement by the new model) really so significant? Shouldn't the quality of the fit be put on a quantitative basis? There are well established quantities describing the quality of the fit (like the profile R-value in powder x-ray diffraction) which could be used.
Related to the question of data quality, the sentence on page 5 (2nd paragraph) 'Since many diffraction spectra suffer from experimental error , we show elsewhere  that there are and we can use these to select a relatively error free l-interval' is really not acceptable as long as reference  is an unpublished manuscript by the authors of the present manuscript themselves. Such operations on the data itself need to be discussed in the manuscript because they are necessary to judge on the validity of the results.
Possibly, model-data (from an artificial stochastic model with known types and volume fractions of different stacking variants) with superimposed systematic / stochastic errors, data evaluation and subsequent sensitivity analysis for the various parameters would be an elegant way out of the problem of limited data quality as long as the demonstration of the power of the method itself is the issue. That could really convince the reader that the method of Varn et al. constitutes an improvement compared to previous approaches.
Such a systematic study would, however, certainly go beyond the purpose and size of a letter.
Given these problems, I recommend to finish the extended and detailed publication (ref. 19 of the manuscript) and have it published first. Once the method in all relevant details - including the influence of possible experimental errors - is publicly available, outstanding results for specific compounds of broader interest could be a suitable subject for a P.R. Letter.
For the present manuscript, I have to recommend to reject it for publication as a P.R.L. for the abovementioned reasons.