I think the presentation has benefitted from the revisions made by the authors.  Below is a list of comments on details regarding terminology and presentation that the authors may want to consider.

p. 1, Abstract first sentence. Resurrection experiments can detect correlations between trait modifications and changes in the environment, but this is not really a test of a causation, is it? Or is the argument here that simultaneous parallel changes in many populations indicate a change in the environment acting over a large area? This could be indicated with a slight rewording.

p. 1, Abstract first sentence. Change “traits modifications” to “trait modifications”.

p. 2, first paragraph. Not fully clear what the important difference is between experimental and natural populations. In both cases, an estimate of effective population size is required.

p. 2, right column, line 3. What does “>0.5” refer to? A broad-sense heritability estimate?

p. 2, right column, line 27. Insert “selfing” after “predominantly”.

p. 2, right column, line 36, “across 22 generations”. Does this species have any seed bank that may affect “effective generation time”?

p. 2, right column, line 47, “taking into account the multilocus genotypic composition…”. Unclear how this should be understood. Reword?

p. 2, right column, line 50, “for neutrality”. I suggest the authors indicate how this is achieved. – By using estimates of genotypic values for flowering time and assuming flowering time is a neutral trait?

p. 3, first paragraph. I still find the procedure for building “families of full sibs” unclear: I suggest the authors state explicitly whether the families multiplied in 2011 each originated from a different pod collected in the field, or whether the families originated from seeds that had been randomly selected from pooled samples of seeds from 1987 and 2009, respectively.

p. 3, right column, paragraph “Temporal changes in sensitivity to vernalization”, “measured as the slope…” This needs some more explanation. Are differences calculated between all possible pairs of plants in the two treatments?

p. 4, third paragraph, “good approximation of the additive genetic covariance”. What about maternal environmental and genetic effects?

p. 4, right column, first paragraph. State explicitly that the individuals analysed represented 145 different families?

p. 5, second paragraph, “As a preliminary step,…”. To me the argument would make more sense in the reverse order, as the changes in flowering time and MLG frequency between 1987 and 2009 are the most direct estimates of evolutionary change. In other words, starting from the observation of the changes in flowering time and MLG frequency, one can examine the strength of the association between flowering time and MLG in the greenhouse, and whether the change is consistent with selection observed in the greenhouse. I see no a priori reason why selection on flowering time in the greenhouse should mirror that at the site of the focal population. To make this order of logic clear, the authors may want to move the description of the selection gradient analyses to after this argument has been formulated.

p. 5, second paragraph, “whether selection in quantified in the greenhouse is likely to mirror selection in the field at present and 22 years ago”. To be strict , it would only need to mirror the predominant selection between 1987 to 2009 to be correlated with the change observed, right? Current selection in the field should matter little?

p. 5, second paragraph, “We then measured…”. I like this approach! The authors should indicate which measure of flowering time was used in this analysis. The legend of Fig. 3 speaks about “average flowering time”. The sensitivity to vernalization treatment varied among genotypes. Are the results of this analysis essentially the same if the analysis is conducted separately for treatment 1 or 2, or separately for estimates of flowering time obtained based on the seed sample from 1987 and from 2009, respectively? 

p. 6, first paragraph; Table 3. Since a single line was sampled in each population, it is a bit misleading to call the examined effect a “population effect”. Change to “line effect”?

p. 7, first paragraph, “predict an evolution of towards earlier flowering”. Since estimates of selection and heritabilities are specific to a given environment, this prediction is valid for the greenhouse and not necessarily for other environments.

p. 7. Was there an effect of year of sampling on estimates of flowering time for MLGs sampled in both 1987 and 2009?

p. 7, right column, second paragraph, “were persistent through time”. Change to “were observed in both years” to make the fact that altogether 5 lines were observed in both the 1987 and 2009 sampling more obvious?

p. 7, right column, second paragraph, “Fig. 3A, regression only significant…”. Add sample size (i.e., number of family means included in this regression).

p. 11, second paragraph, “Munguia-Rosas et al.”. Note that selection estimates considered in this meta-analysis largely ignores the effect of variation in number of flowers and plant size, suggesting that many of them rather reflect a correlation between plant condition and fitness.

Finally, I suggest the authors somewhere add a caveat regarding possible G x E interactions for flowering time (greenhouse vs. field), when discussing the possible association between flowering time as expressed in the greenhouse and fitness and evolutionary change in the field. 

I am satisfied with the answers to my comments and with the modifications to the main text. The qqplots should be added to the supplementary figures linked to main figure 3.

The study by Gay et al. reports empirical data on the evolution of flowering time in a highly selfing species: Medicago truncatula. The authors used several approach to investigate the question. In particular, they used a resurrection approach with seeds from 1987 and 2009. The aim of the study is to disentangle the role of drift and selection in the shift observed as well as estimating selection gradient of flowering time. The study is interesting and the different experiments (pop centered, regional) is consistent with a shift in flowering time. Below, my comments:

1-The introduction discuss the question of adaptation face to environmental change. While the text is rich and well referenced, I found that the introduction is a bit long. There is a long discussion on whether outcrossing/selfing traits influences adaptation. The logical consequence would be to compare outcrossing/selfing populations. Since the study does not compare outcrossing and selfing populations, I think this part should be greatly reduced. Also, the statement that bottlenecks are more frequent in selfers (if true !!) would be more striking if the references were reporting empirical data. To my knowledge, Schoen and Brown (1991) and Ingvargsson 2002 hypothesize that it is the case but did not demonstrated that selfers suffer from higher bottlenecks. In the following paragraph, I found confusing to assert that “self-fertilization mays have facilitated adaptations to agricultural practices” when discussing the role of mating system on adaptation. Is it because the traits were preadapted or because the genetic architecture of selfers facilitates adaptation? In short, the introduction should be more focused to introduce the question short term adaptation of flowering time in the face of warming.

2-Sum of temperature. The individual flowering time is converted in sum of temperature. The basal temperature is assumed to be 5°C, based on Moreau et al (2007). Would it be possible that Tb has evolved during the two decades? Would the conclusions be different if flowering time were measured as the number of days? At least, the possibility of a shift in Tb should be discussed as I found contradictory to evaluate adaptation to warming but keeping Tb constant.

3-Maternal effects. If I understood well, the results on the studied populations are corrected for maternal effects (one generation to refresh seeds stock) but the results of regional analysis are based on the F1 generation (without correcting for maternal effects). I was interested by the amplitude of the shift: two days in the cape Corsica populations but five days in the regional analysis. This may be a “true result” or an effect of correcting for maternal effects. Did the authors measure the flowering date in the F1 of the cape Corsica populations. I would suggest to mention this result in the discussion. Is it possible that the difference in flowering date reported have changed in Cape Corsica population because of the F1 generation in greenhouse? My feeling is that these results are, as such, interesting. We often see this pattern of a lower amplitude after one generation. If it was only noise, the first generation should exhibit either lower or higher difference than the F2. Epigenetic components of flowering could have played a role in adaptation to warming and these effect cannot be distinguished from true quantitative genetic effects if parts of these effects last more than one generation. Do the same MLG (from 1987 and 2009) have the same fitness? Because the authors have the chance to have the same MLG, it would be interesting to look at this relationship to investigate maternal effects.

4-Genetic analysis. If I understood well, the test for selection versus drift is based only on conserved multilocus genotypes, i.e. a fraction of the population. Why doing this choice? Why not using a Qst/Fst approach that would take into account all the individuals? (the design allows to estimate Qst, doesn’t it?). In addition, I see a potential bias because it assumes that the population behaves as a fully selfing populations, which is not the case. While the authors point the potential differential selective response of outcrossers versus selfers, the results reported are based only on the full selfing fraction of the population, which I found contradictory.

Overall, I found the ms interesting and such long term dataset is rare. However, the ms would benefit from being more focused (particularly the introduction) in order to highlight the results and their biological interpretation.

This study uses a resurrection experiment and simulations to explore the possible causes of changes in flowering time and genetic composition of a Medicago truncatula population across 22 generations. In the resurrection experiment, plants grown from seeds collected 22 years apart were raised in the greenhouse to produce selfed lines. These lines were then used to document possible changes in flowering time and to quantify selection on flowering time in the greenhouse. Changes in genetic composition were characterized by scoring 20 microsatellite loci (16 kept after filtering) and documenting changes in the frequencies of multilocus genotypes. The paper is well written and addresses interesting problems of wide general interest. However, I think the authors need to (a) motivate their approach to use estimates of selection obtained in the greenhouse to infer selection in the field, (b) provide more detail on the distribution of multi-locus genotypes and the power of their analysis of change in genetic composition, and (c) clarify a few details when it comes to sampling procedure (see below).

Main comments:

1. The authors appear to assume that selection quantified in the greenhouse is likely to mirror selection in the field at present and 22 years ago. This needs to be motivated.

2. I suggest the authors provide more detail on the distribution multilocus genotype (MLG) frequencies, and that this information is given already at the start of the third paragraph on p. 7. They report that 60 different MLGs were detected in their sample of 145 individuals. Two MLGs were common, and 12 MLGs were shared between the two sampling years. This suggests that most MLGs were rare and perhaps only represented by a single plant? The authors may want to discuss whether their sample sizes are sufficient to characterize changes in genetic composition of a population with such skewed distributions of MLGs.

3. I suggest the authors clarify a few details regarding sampling:

(a) For the resurrection experiment, “100 seeds per sampling were replicated” (p. 3, second paragraph). Were these seeds from 100 different pods and thus sampled from 100 plants, or were they a random sample of 100 seeds from a pooled seed sample from each year?

(b) For the genetic analysis, leaves were sampled from “the multiplication generation in the greenhouse” (p. 4, fifth paragraph), and after filtering 145 individuals remained in the data set to be analysed. Please, state explicitly that the “multiplication generation” refers to the plants derived from the 200 field-collected seeds (presumably representing seeds from 200 plants(?); see previous comment). Were seeds from the two sampling occasions equally represented among the 145 individuals included in the analysis?

Minor corrections:

Abstract, line 11 from bottom. Change “population” to “populations”

p. 7, first paragraph, second line from bottom, “in both years”. From this wording, you easily get the impression that selection was quantified in two years. I suggest you add a few words to indicate that this rather refers to a similar negative relationship being observed among lines derived from each of the two years.

To make text in graphs readable, font size should be increased in Figures (in particular in Figs. 3-5).

In this study, the authors test whether flowering time evolved in an experimental population of Medicago truncatula and whether this change could represent an adaptation to varying environmental conditions. For this, they measure changes in flowering time in a natural population over 22 generations (2 timepoints), they quantify the association between flowering time and fitness (as approximated by the number of seeds produced), they track changes in haplotype frequencies characterized by different approximated fitness values, and finally they also measure changes in flowering time in 17 populations from the same geographical region that have been sampled twice over a comparable time range.

The authors report a significant reduction in flowering in the main population and in the regional analysis that appears to be consistent with the specific effects of climate change in the Mediterranean region (i.e. limiting summer drought occurs earlier in the year). They also report a significant association between flowering time and seed production. However, the evidence for the effect of positive selection obtained by analyzing the changes in haplotypes is at best marginal; even if the authors do a good job in describing some of the uncertainty associated with this analysis, I think that one more aspect should be exposed.

Besides my major comment, I find the manuscript clearly written, the analyses carefully conducted and presented, and the intro and discussion very well written and informative, at least for the non-expert.

Major comment

My only major criticism refers to the results presented in Figure 3. The selection gradients measured here seem to be heavily influenced by two outlier points with low seed production and early flowering. As a result, the linear models (especially the one for MLG found in 1987) appear to be a poor fit to the data, as can probably be seen by inspecting the residuals, which are unlikely to be normally distributed. I think that the authors should report the uncertainty around the slopes and that this uncertainty should be further considered in the analyses presented in figure 4, which will likely cause the observed selection gradient to be non-significant under a larger range of Ne values. I am not sure about the best way to obtain confidence intervals for the selection gradients but I imagine that a bootstrap approach should be applicable.

Minor

I agree with the authors that the N_e value estimated from the temporal Fst is very likely underestimated. Comparing the expect heterozygosity under Ne=19 with the observed He would further support the idea that larger Ne values are indeed realistic. How does the observed heterozygosity in the population compares to the theoretical expectations given by Nordborg and Donnelly (1997)? Rescaling the census number (>2000) by 1/(1+F) would lead to a less conservative Ne value for the test for selection and may allow a putative selection signal to be detected even after considering the uncertainty around the observed selection gradient.