Referee 2's review:

Review of Rozen et al. "Heterogeneous adaptive trajectories of small populations on complex landscapes".

I think this manuscript describes results from a very interesting experiment - one of very few that attempt to directly test an interaction between environmental complexity and population size (mutation supply) in influencing evolutionary trajectories. However, in its current form I think the conclusions made by the authors are too strong for the experimental evidence. In particular, I am not convinced that the central claims of the paper, that greater exploration of the genetic landscape can occur because large fitness effect mutations are unavailable and that this exploration can lead to higher fitness, are fully supported by the reported results. Nevertheless, I am sure the results of this study will be of general interest and I support its publication if the points raised below can be addressed.

1. As alluded to by the authors, it is more difficult to reject null hypotheses when the number of replicate populations analyzed is small (as in the 'large' treatments). (This problem is particularly relevant to interpreting the findings of less among-population genetic variance in fitness and more parallelism in adaptive trajectories, among large populations.) In principle, therefore, I agree with the authors emphasis on those tests that attempt to compare among-population variance and mean fitness improvement between 'large' and 'small' treatments. However, I am not sure I understand these tests fully. First, exactly what test was done to compare the among-population variation in fitness across the 'small' and 'large' treatments? This test is not described, and the degrees of freedom given in the accompanying F statistic don't make sense to me (if two treatments are compared, why isn't the numerator '1'?). Similarly, I am concerned that I don't understand the degrees of freedom associated with the t-statistic reported when the fitness means are compared - I'm not sure exactly how the tests are being preformed. I would like to see ANOVA tables detailing all analyses that are reported - at the very least, the factors presented as P values should be detailed in the text. Second, it is not clear to me how bootstrapping from the 'small' population treatments to create the same number of pseudo-populations as were originally present would be expected to have any great effect on the calculated variance or mean. If they don't, I can't see how this strategy addresses the original imbalance in sample size. I readily admit that I don't know these statistics, but I would like to see at least some explanation for this test and how it should address the particular imbalance present in this manuscript. In short, I can believe that the bootstrap tests the 'robustness' of the reported results, but I am not sure it addresses the underlying imbalance in sample size. Also: (1) eye-balling the data, I would think that any test should address the influence of one outlying point among the small-complex populations and I don't see how the bootstrap will do this, and (2) I don't see why you should bootstrap the 'large' populations. Finally, have the authors considered applying non-parametric statistics, at least as a conservative, and therefore, compelling, complement?

2. Not withstanding my reservations about the statistical tests used to describe the experimental results, my main reservation about this paper is whether these results would in any case be strong enough to justify the claim of a causal link between greater exploration of an adaptive landscape in the small populations, and higher eventual fitness. To establish this link, I would like to see the points and alternatives below addressed.

A. The mechanism proposed to allow for greater exploration of the adaptive landscape in small populations predicts that beneficial mutation in these populations will (must) be smaller than in large populations. Clearly, this is a difficult prediction to test, but I find it difficult to reconcile those results that are reported in the manuscript with this prediction. For example, in the complex environment, fitness improvements of up to 15% were seen in several of the small populations after only 100 generations - no formal comparison was made, but this seems at least as high as the initial gains made by the large populations. After only 100 generations, I wouldn't think that more than one mutation would be likely to be present in any given individual in a population, together with the fact that little, if any, further improvements seem to have been made by most populations, I don't follow how it can be said that the small populations have substituted smaller mutations - if they haven't, what is the mechanism by which they have explored more of the adaptive landscape?

B. A second requirement of the mechanism proposed to explain higher fitness in small vs. large populations evolved in the complex environment is that multiple adaptive peaks exist in this environment. As far as I can see no evidence is presented to support this. Divergence is found in this study (again, subject to the authors addressing the concerns raised above) and in one previous study (Habets et al., 2006) - but it is not clear to me how the authors distinguish between this indicating that populations have diverged to distinct peaks vs. them being at different points along the same/different trajectories to the same peak. A formal test to examine whether fitness has levelled off in the evolving populations - indicating that they have reached their respective adaptive peaks, could clarify this issue.

C. Have non-transitive adaptations evolved in any environment? If so, these could make interpretation of a rate of adaptation by reference to competitive ability with the ancestor misleading. I would like to see if the authors have any thoughts on whether non-transitivity may have evolved and if so, what effect it may have. (Have any simple or complex evolved populations evolved differences in colony morphology?)


Minor points:
In several places in the manuscript I find the terminology somewhat vague or confusing. For example: are small populations 'evolutionarily' or 'adaptively' handicapped (abstract)? What is meant by the phrase 'Reaching the global optimum on rugged landscapes is expected to be a function of the specific mutations that are substituted' - won't reaching a global optimum always depend on the mutations that are fixed (p2-3)? Specifically, what are 'these' suppositions (/predictions?) (p3)?

Consider introducing the processes described by 'phase 1 and 2' of the shifting balance theory when they are introduced.

P3, paragraph 1. Do the authors know of any direct evidence that small populations substitute mutations with a wider range (as opposed to simply smaller on average) of fitness effects than do large populations? If so, I would like to see the relevant reference cited. The only study I am aware of that has looked directly at this question does not, as far as I can tell, support this claim (Perfeito et al., Science 317: 813-815).

P3. LB stands for Lysis Broth - not Luria-Bertani Broth.

P4, paragraph 1. Why is t statistic reported with a denominator?

P4, paragraph 1. Typo? The results of t-tests between small and large populations in the two treatments are exactly the same.

P4, paragraph 2. Why is the test for parallelism using the subset of small populations now a t-test?

Model and p9. I think there has been a conversion error 'u' has turned into '!'.

Although I think the simulation model is interesting, and I don't have any specific issue with it, I am not sure it helps this paper. The results of the model aren't reported in a way that shed any additional light on the underlying mechanisms of the experimental results - instead it 'merely' supports the experimental results.

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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.