Referee 4's Review:

In this manuscript the authors use new as well as previously published data on stick insect taxa to test the 'niche dimensionality hypothesis'. This hypothesis states that divergent selection between taxa along multiple niche dimensions promotes the evolution of reproductive isolation. The authors find support for the hypothesis, in that reproductively non-isolated host plant ecotypes of Timena cristinae and of T. podura are exposed to divergent selection mainly on coloration, whereas the two established species T. podura and T. chumash, which differ in their host plants, are exposed to divergent selection on both coloration and on host-plant-related physiology or performance. There is no doubt in my mind that the niche dimensionality hypothesis is potentially important, and thus well worth testing. The reported field experiments on survival and performance on the different host plants are ambitiously planned and seem well executed, adding to the quality of the study. Thus, I am generally in favor of this work, although I also have a number of questions and comments.

1. Because the study only involves one species pair, for which there seems to be limited information about their evolutionary relationship, it can at best provide rather weak and circumstantial evidence in favor of the hypothesis. The authors are clearly aware of this, and do not extend their interpretations in an unreasonable way. However, I am still a bit dissatisfied with the almost complete lack of mention of the phylogenetic history of host plant relationships in Timena, and in in particular with the lack of this kind of discussion for the podura/chumash species pair. Is feeding on either Ceanothus or Adenostoma primitive in Timena, and which plant was the likely host of the ancestor of T. podura and T. chumash? This kind of information would be needed to evaluate whether currently observed interspecific differences in host-plant performance are at all likely to be involved as causal agents for the evolution of reproductive isolation. On this crucial matter, the authors have rather little to say. I think they should either admit that nothing is known about the phylogenetic history of host use, or provide whatever information there is on the subject.

2. The authors report a greater magnitude of divergence in stripe-body brightness contrast between species than between ecotypes (bottom p. 7 and Fig. 1). Looking at Fig. 1, I was a bit surprised by this, since there appears to be a more distinctive dorsal stripe on the T. chumash image than on the image of the Ceanothus ecotype of T. cristinae (Fig. 1A), whereas Fig. 1B seems to suggest an almost absence of a dorsal stripe on T. chumash. The images are of course just of single specimens, but a possible explanation may be found in the data on hue and saturation in Table 1, where it seems that T. chumash indeed has a more pronounced dorsal stripe than the C ecotype of T. cristinae. In view of this, is it really fair to emphasize (p. 7, lines 27-28) a greater interspecific divergence in coloration? Is there any strong basis for such a view? I am also a bit uncertain about including morphological data in Table 1, or at least putting this data into the same PC analysis. Why not perform the PC analysis only on coloration, which would seem to be most directly related to crypsis on the host plant?

3. I am a bit confused by the T. chumash data in Fig. 2A. The two bars do not sum to 100% (the bar with 4 individuals seems too tall).

4. Table 2 is very big, and I do not think it is necessary to include it (on the other hand, it does not do any harm).

5. In responding and adjusting to previous comments, the authors have introduced a slightly defensive tone into their writing. This is perhaps not a big problem, but in my view it is more important to be clear about the strength or weakness of the test of the niche dimensionality hypothesis that has been conducted. I think the present results are mainly suggestive, and the role of divergent selection along multiple niche dimensions as a causal factor for the evolution of reproductive isolation is not at all established, or even directly supported, in this study.

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N.B. These are the comments made by the referee when reviewing an earlier version of this paper. Prior to publication the manuscript has been revised in light of these comments and to address other editorial requirements.