Technical Comments

Response to Comments on “Bateman in Nature: Predation on Offspring Reduces the Potential for Sexual Selection”

Science  03 May 2013:
Vol. 340, Issue 6132, pp. 549
DOI: 10.1126/science.1233500


Commenters objected to the way that we counted matings and offspring to calculate Bateman slopes and disagreed with our contention that predation on offspring can decrease the potential for sexual selection. We clarify what may have been misunderstandings to argue that our methods, analyses, and conclusions are correct.

The Comment authors (13) made four main criticisms of our article: (i) that we did not count matings appropriately; (ii) that we did not count offspring appropriately; (iii) that the relationship between the Bateman slope and offspring mortality was automatic, given the way that we counted offspring; and (iv) that we did not relativize matings and offspring before computing the yearly Bateman slope.

Arnqvist (1) claimed that we could have obtained better estimates of matings by observing copulations. Copulation duration in pronghorn is approximately one second, and copulations are dispersed in space and clumped in time (4). We rarely observe a female who mates more than once per estrus. This is why the discovery of some multiple matings, inferred by paternity analysis, came as a surprise. Reliable observation of all copulations is not possible in our system, nor is it in most species. A fair reading of the literature in behavioral ecology suggests that observing copulations is a notoriously poor way to estimate male number of mates (5). However, it is possible for us to capture nearly all of the pronghorn fawns that are born each year and to assign a sire to each at 95% confidence. We contend that this provides the best possible estimate of male number of mates. Arnqvist claimed that pronghorn females often mate multiply, citing one of our earlier publications. The data reported in that publication were derived from paternity analyses, conducted over two breeding seasons, which used eight microsatellite loci and accepted 80% confidence in paternity assignment (6). In the data set represented in our report, we used 19 microsatellite loci, and all paternity assignments were at 95% confidence. In this sample of 273 litters, 241 (88%) were full siblings (same sire) and 32 (12%) were half siblings (different sires). Of these 32, we observed only six instances of multiple mating. The frequency of multiple mating is not high, but it is higher than what one can observe. The best way to estimate male number of mates is to use genetic paternity assignment (7).

A second objection made by all three commentators concerned the age at which we counted offspring as “produced.” Objections here reflect a widespread controversy on when units of reproduction should be counted to assign fitness (8). We contend that one can only estimate the maximum possible strength of sexual selection by recording recruited offspring. Traits that give males a mating advantage can only increase in frequency when the offspring of those males are recruited. That is one of the main points of our manuscript.

Also, in pronghorn, offspring numbers change between fertilization and the age at recruitment (9). At estrus, females ovulate about seven eggs, and all are fertilized. Mortality among blastocysts results in reduction to four embryos that implant. Subsequently, each distally implanted embryo sends a sheath of necrotic extra-embryonic membranes that pierces and kills the proximally implanted embryos. Then, after birth, predation by coyotes kills many young. There are several stages, separated by bouts of mortality, between fertilization and recruitment. At which of these stages should we count offspring? We contend that the minimum age of recruitment is by far the least ambiguous of any number of time points, separated by mortality, at which one might count offspring, and it also is the best way to count if one wants to measure the real opportunity for sexual selection.

Imagine a species in which males have an ornament, such as a long feather, that they display in courtship. We observe that females prefer males with long feathers and that long-feathered males gain most of the matings. We count chicks at hatch and calculate a Bateman slope of 1 (perfect correspondence between male mating success and offspring produced). We conclude that sexual selection is operating strongly on feather length. However, we do not follow chicks after hatch, and thus we do not detect that predators kill 80 to 90% of them before fledging. We would then be confused when we failed to measure any increase in tail length between generations. We might falsely conclude that additive genetic variance for feather was absent. One of the main conclusions from our article is that the appropriate way to count offspring to calculate the Bateman slope is to count offspring at the age of recruitment.

The Comment authors claimed that because we counted offspring at the age of recruitment, the relationship between fawn mortality and the Bateman slope became automatic. We disagree. It was not possible to predict, a priori, how patterns of fawn mortality would fall on the skewed distribution of fawns produced.

For example, we showed previously that, in our study population, there is a sire effect on offspring survival. The most frequently chosen sires produce offspring with higher probabilities of survival than the offspring of the least frequently chosen sires, likely due to a sire effect on offspring growth rates (10). In addition, the structure of breeding age females changed across study years, and older female pronghorn have higher rates of offspring survival (4). Thus, it was possible that the Bateman slope would have had a weaker relationship, or no relationship, to the magnitude of fawn mortality.

Comment authors claimed that we should have relativized matings and fawns recruited before we calculated the Bateman slope for each year. However, it is not clear why one should do this when working within the same population, and our analysis was the same as that done in most modern reports of Bateman statistics, including one published by Bergeron (1114).

Ramm et al. (3) wrote that we overstated the interpretation of our analysis done to evaluate the random effects hypothesis. However, ours is the first test in nature of this challenge to Bateman principles, and we contend that we have indeed shown that random effects could not have generated the observed variance in male mating success.

Finally, one Comment (3) criticized our use of a generalized linear model (GLM) with six independent variables when we had 10 years of data. They contend that this procedure may have spuriously obscured other significant effects. To evaluate this objection, we ran six separate bivariate linear regressions (a procedure with its own set of problems, which the GLM is designed to avoid) and obtained the same result as in our table 2 (8).


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