Home > Methodology, Sex/Gender Differences, The Body, The Face > No Evidence of the Good Genes Hypothesis Found

No Evidence of the Good Genes Hypothesis Found

February 20, 2009 Leave a comment Go to comments

Using photographs of real men, Peters, et.al (2009) found no evidence of a preference for either masculinized or symmetric male faces or bodies in ovulating women.

Previous studies that have found a relationship between ovulation and attraction to masculine features have used computer-morphed images that are weak in ecological validity. This study used photographs of actual men, like the ones below.

Masculinity, attractiveness, and symmetry ratings of the stimuli appear to approximate a normal distribution, strengthening the ecological validity of this study. The only noteworthy limitation in this design is that there were no objective measurements of masculinity or symmetry – only subjective ratings were used.

The authors were also careful to use precise measurements of ovulation to ensure that the ratings of women in the ovulatory phase were well-within the previously identified six-day long sexually active phase of the menstrual cycle.

Wayne Hooke

Marianne Peters, Leigh W. Simmons, Gillian Rhodes (2009). Preferences across the Menstrual Cycle for Masculinity and Symmetry in Photographs of Male Faces and Bodies PLoS ONE, 4 (1) DOI: 10.1371/journal.pone.0004138

  1. February 27, 2009 at 10:39 am

    Hi. Did you see this article/research? (Link goes to my comment on article…)


    • whooke
      March 2, 2009 at 8:37 am

      I haven’t read the actual article – just the Wired piece. I’ve been swamped with committee work, preparation for my last go-round prior to getting – or not getting – a continuous appointment at my institution (sort of like tenure); and slowed-down by several cold/flu bugs. Certainly interesting – definitely preliminary.

  2. Nadia
    May 19, 2009 at 12:51 pm

    You might be interested in this paper which also uses real faces and a rating scale:

    Roney, J. R., & Simmons, Z. L. (2008). Women’s estradiol predicts preference for facial cues of men’s testosterone. Hormones and Behavior, 53, 14-19.

    • whooke
      May 25, 2009 at 12:30 pm

      Thanks for the suggestion! I’ll follow-up in a couple of weeks when the term is over!


  3. Skeptic
    June 28, 2009 at 11:24 am

    “Previous studies that have found a relationship between ovulation and attraction to masculine features have used computer-morphed images that are weak in ecological validity. This study used photographs of actual men, like the ones below.”

    It’s not true that previous studies that found a relationship between ovulation and attraction to masculine/dominant men used only computer-morphed images or stimuli that were weak in ecological validity (as this article implies).

    Gangestad and colleagues’ study from 2004 used video clips of men and found an effect of ovulation. Surely video clips have greater ecological validity than face photographs of the type shown in this article or bodies with their heads cut off!

    As well as the facial studies the article mentions, effects of ovulation on attraction to masculine characteristics have been shown in studies of voices, gait, pheromones…….it’s a real stretch to think that this one study changes things much.

    And this study shows an effect of ovulation on masculinity preference using photos of real men:

    Little, A. C., Jones, B. C. & DeBruine, L. M. (2008). Preferences for variation in masculinity in real male faces change across the menstrual cycle. Personality and Individual Differences, 45, 478-482.

    • whooke
      July 9, 2009 at 12:01 pm

      Hi Skeptic,

      I’m going to stick to my guns on this one, with one correction: the Little study you cite does use photographs of real men and does report a cyclical preference for masculinized faces. I will confess that I overlooked this one, but, upon review, I don’t know what it adds to the research…. Some of my concerns with this study are:

      – there are no objective measures of ovulation or masculinity

      – the average masculinity rating of the faces in the high masculinity stimulus set was 4.05 on a 7-point scale: which is much lower than what has been found attractive in other studies. Essentially, this forced-choice study compares low perceived masculinity faces with medium perceived masculinity faces

      – male ratings were used in creating the high/low masculinity stimulus set, but not in the experimental condition. The r-value of .722 between the male/female ratings in the creation of the stimulus set leaves quite a bit of the variance in male/female ratings unaccounted for and there’s no way to be sure what influence this might have on the experimental results

      – no actual images are available for viewing: when it comes to beauty studies, I like to see at least some of the stimulus set

      More broadly, I remain very sceptical of the good genes hypothesis’ explanation for estrous-like effects in human females, not of estrous-like effects generally.

      • Skeptic
        July 9, 2009 at 12:30 pm

        I’m a bit puzzled by some of your comments here to be honest.

        1. You criticize the little study for not using objective measures of masculinity, but neither does the Peters study that you cite. Similarly, while you criticize the Little study for having no objective measure of ovulation, the classification of women in this study was sufficiently accurate to yield a significant effect. Since misclassfication would simply add noise to the data, it’s very difficult for me to see how misclassifcation alone could cause an effect. Perhaps if the Little study was the only one to show this type of effect, then I could see your point. But I find it hard to believe that all of the studies reporting effects of menstrual cycle phase on preferences for masculine faces, voices, videos of behavior and odour are all artifacts of misclassification.

        2. You say that “Essentially, this forced-choice study compares low perceived masculinity faces with medium perceived masculinity faces”. Nonetheless, medium levels of masculinity are still more masculine than low levels. Consequently, the Little study shows that women’s preferences for more masculine faces are stronger around ovulation than at other times.

        3. You criticize the Little study because male and female raters rated the stimuli for masculinity. But this criticism ignores the high inter-rater agreement for these ratings (Cronbach’s alpha=0.98) which is actually higher than that in Peters’ study. Given that previous research shows that both men’s and women’s ratings of male facial masculinity correlate with objective measures, I can’t really see how the inclusion of male raters for masculinity presents a problem.

        4. I disagree that seeing an example image is particularly informative about an image set.

      • Skeptic
        July 9, 2009 at 12:33 pm

        sorry, I meant to respond to this point too:

        “More broadly, I remain very sceptical of the good genes hypothesis’ explanation for estrous-like effects in human females, not of estrous-like effects generally.”

        I agree that skepticism is useful (as my name implies!). But, given the number of studies on this topic that report significant effects across a wide range of domains (face, voice, videos of behavior, trait descriptions, odours), I also don’t think it wise to attach much importance to a single null finding.

  4. whooke
    July 9, 2009 at 3:45 pm

    Hi Sceptic,

    It looks like we have two areas of disagreement: the impact of the Little study and the status of the good genes hypothesis.

    The Little study’s explicit purpose is to expand the connection between cyclic preference shifts in human females and unretouched photographs of male faces – given that previous research has found a preference shift using retouched images. Little used unretouched photographs – which adds an element to the body of research. However, I have concerns about the stimulus set: the subjective masculinity ratings of the male raters correlate with that of female raters at r = .722; which sort of means that we can assume that about 50% of the variance in the female raters’ masculinity ratings is explained by the male raters’ masculinity ratings. That leaves 50% unaccounted for. Using standard measurement theory, noise can be random or systematic. Given that there is a sex difference here, there could be systematic error. For me, that is a significant caution that makes drawing conclusions from this study difficult.

    Little essentially used the calendar method (with self-report)for determining location in the ovulatory cycle. As a method of birth control, the calendar method has a yearly failure rate of 25%….

    In the end, the study maybe shows something new…. maybe it doesn’t…. for me, it is too loose to add significantly to the discussion. The study was published in a peer reviewed journal, though, so, you’re not the only one who evaluates it more significantly than I.

    I disagree wholeheartedly with you about the status of the good genes hypothesis. The good genes hypothesis essentially argues that fertile women prefer high androgen males because androgens are a handicap and the display of androgenized features advertises good genes. As of 2005, the Weeden meta-analysis found little substantive evidence for a connection between male attractiveness and health. Further, the carte blanche application of the handicap principle to human attractiveness research is wildly premature (Getty, T. (2002). Signaling health versus parasites. American Naturalist, 159,363–371.). For example, if testosterone facilitates predator avoidance and predator avoidance is more signifcant than parasite resistance, testosterone is not a handicap.

    Some cyclic variation in human female mating behavior is well documented. I do not disagree with this conclusion. What I disagree with is using the good genes hypothesis as the explanation for what’s been found.

    Best Wishes,


  5. Nadia
    July 10, 2009 at 7:23 am

    I broadly agree with your response, and wanted to add a couple of things. The Weeden meta-analysis found little evidence that overall male facial attractiveness was linked with health, but it did find that male facial masculinity was linked to health based on the Rhodes et. al 2003 paper. Moreover, another study found the same relationship (Thornhill and Gangestad 2006). Again, no linkage between male facial attractiveness and health but a linkage between sexual dimorphism and health.

    Subjective ratings do have minuses, but Thornhill and Gangestad and Rhodes et. al 2003 found similar effects using measured versus subjective ratings.

    “Face masculinity/femininity in men. Men’s face masculinity
    has the unlikely outcome of not typically predicting
    attractiveness judgments but
    predicting modestly (in a single study) health outcomes (r
    = .17).”

    (By the way on the Weeden/Sabini analysis, is focused on Western societies. There is some indication that their findings with respect to BMI and women do not hold up around the world. Swami and Tovee found that different ethnic groups tend to have similar preferences for BMI, despite having different optimal BMIs for health. Moreover, there may be some indication that in East Asia, young men prefer women with BMIs that are not ideal for health. Swami et. al found that 18 was the preferred BMI in Japan, but public health data suggested 21-22 was the best for health.)

    V. Swami & M.J. Tovée. Female physical attractiveness in Britain and Malaysia: A cross-cultural study. Body Image 2005, 2, 115-128.

    V. Swami C. Caprario, M.J. Tovée & A. Furnham. Female physical attractiveness in Britain and Japan: A cross-cultural study. European Journal of Personality 2006, 20, 69-81.

    That said, I broadly agree with your reaction to the Little et. al study. Also, the authors forced viewers to choose between two faces matched for attractiveness. This is ideal for finding an effect, but it doesn’t answer a crucial question: how large or important it is. Along these lines, another purported effect is that more attractive women find masculinity attractive. Yet, a recent study, found no greater propensity for such women to actually marry masculine men (and the authors did predict that such women would be partnered with masculine men). It’s debatable how much visual preferences translate into mate choice, but if these effects are very subtle, then it’s unsurprising.

    Sexy sons and sexy daughters: the influence of parents’facial characteristics on offspring
    Animal Behaviour, Volume 76, Issue 6, December 2008, Pages 1843-1853

    I think if these effects exist, they are likely quite small and subtle and have little effect on social cognition in most situations.

    • Skeptic
      July 10, 2009 at 7:34 am

      A point that’s relevant to this issue: “It’s debatable how much visual preferences translate into mate choice, but if these effects are very subtle, then it’s unsurprising.”

      DeBruine et al. (2006 Proceedings of the Royal Society of London) finds that women’s ratings of the masculinity of their current romantic partner are positively correlated with the strength of their preferences for masculinity in men’s faces (assessed using a forced choice method). So, even with a forced choice method, women’s visual preferences do appear to predict their mate choices.

      • Nadia
        July 10, 2009 at 8:11 am

        As Peters et. al points out that study may have been biased by the fact that the women evaluated their own partners. They were not externally assessed by ratings or objectively assessed by measurements. In the Perrett and Cornwell paper, the photographs are evaluated by raters, not by the wives themselves.

    • Skeptic
      July 11, 2009 at 3:02 am


      As Cornwell and Perrett note, though, they don’t have a strong test for their predictions concerning male masculinity because their sample were selected for being in very stable, long-term relationships, potentially biasing against effects of masculinity on mate preferences and choice. This bias would not affect the attractiveness correlations that they found and report. It seems strange to accept at face value a null finding when the authors themselves acknowledge that they don’t have a strong test for that hypothesis.

      As for the DeBruine study, I don’t really see how their approach could bias the results in the sense of generating a (false) positive correlation.

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