I sent your paper to three expert referees, and have now heard back from all three. Referee R1 (“This paper proposes and tests…”) likes a number of aspects of the theoretical analysis, but is concerned about the extent to which the data can fully speak to the model, and is skeptical overall that the paper’s contribution clears the bar for the AER. This referee recommends rejection. Referee R2 (“Empirically the paper looks at…”) raises questions about the mechanism underlying the matching in your model, and also questions some of the connections between the theory and the empirical analysis. This referee recommends a revise in resubmit, but notes in their cover letter to me that they intend this as a “weak R&R.” Finally, referee R3 (“This is an ambitious and well-crafted paper…”) appreciates the effort to incorporate genetics into economics, though this referee questions the novelty of some aspects of the theoretical analysis, and again questions some aspects of the empirics. This referee recommends rejection.
I have also read the paper myself, and find that I share some of the concerns raised by the referees. In particular, while I do not know the genetics literature well, based based on the papers highlighted by R3 I do think it would be helpful to spell out more explicitly how you think about the paper’s contribution relative to the literature that the referee flags. In addition, I share some of the concerns voiced by all three referees about the empirical specifications and results in the paper. While I recognize that some of these concerns stem from the structure of your data and may be difficult to address, given that similar concerns were raised by multiple referees I think that incremental progress here could be quite helpful. Overall, I do not see a path forward for the paper at the AER, and so have decided to reject.
Literature!!!
Empirics, make our case more strongly esp on robustness to specifications
Theory-empirics connection
Comments to the Author
This paper proposes and tests a hypothesis about assortative mating, namely that both social status and genetics contribute to a person’s attractiveness in marriage markets. Therefore, wealthier people marry persons with “better” genes leading their children to inherit both wealth and genetic variants associated with better outcomes such as higher intelligence. The authors refer to this process as social-genetic assortative mating (SGAM). They develop a theoretic model to show that social-genetic assortative mating in one generation increases the correlation between SES and genetic variants in the offspring generation and, hence, increases the intergenerational persistence of SES. The empirical analysis shows that persons that have higher education or income are more likely to marry persons with genes that are predictive of high educational achievement. They also show that higher birth order is negatively related to marrying a person with genes that are predictive of high educational achievement (measured by PSEA score). The data come from the UK Biobank. This is a very interesting paper that has a nice combination of theory and empirical analysis. Comments:
- The theoretical model has many interesting implications most notably about patterns of intergenerational transmission and how they vary across different types of societies. Unfortunately, due to data limitations, the authors are not able to study intergenerational linkages and this limits the capacity of the empirical work to speak to the theoretical model. The authors focus on one particular prediction – that higher SES individuals are likely to have spouses that have “better” genes, conditional on their own genetic makeup.
don't think we can do much about this, except clarify the move from theory to empirics as which implication we test
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While the data have considerable strengths, they also have some weaknesses. The sample is not a random sample and spouses are matched with some error (which happily appears small).
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Figure 4 shows a general pattern that higher SES individuals have spouses with higher PSEA scores. As the authors point out, this is unsurprising given the findings from the large literature on assortative mating. What they want to test is, conditional on own genetic makeup, are higher SES individuals more likely to match with spouses with higher PSEA. To do this, they use birth order as a source of exogenous variation in SES, conditional on genetic makeup. I am not wholly convinced by this strategy. A typical assortative mating story might argue that people often meet spouses in education so, if you go to college, you are more likely to marry a college graduate (Kirkeboen et al., 2021). First-born children are more likely to go to college and so are more likely to marry a college graduate. College graduates will both tend to be from higher SES backgrounds and have higher PSEA scores than others. So, first-borns will be more likely to have spouses with higher PSEA scores. If this is what is happening, it is not clear how exactly it relates to the theoretical model in the paper.
I don't understand this criticism but again need to clarify theory/empirics link.
- I think the birth order specification would benefit from further discussion. There is now an enormous empirical literature on birth order and an effort should be made to match up the specification to best practice in the literature. One control variable that should be included in the current specification, if it is available, is age of the parent at first birth as it is correlated with birth order once one conditions on the age of the parent at the birth of the child.
Alas not possible. But can discuss more generally what we already know.
For reasons such as this, the literature generally does regressions with family fixed effects to eliminate any possibility that birth order is correlated with characteristics of the family. In the literature, the sample is usually restricted to families with 2 or more children, and variables are included for the exact birth order (2nd born, 3rd born, 4th born, etc.). Further heterogeneity is usually allowed by doing separate regressions by family size.
All of that we've done, but maybe need to make clearer, speak slowly and loudly, etc.... Perhaps we can explicitly discuss the results with dummies in the main paper.
The lack of information on deceased parents is a potential issue as it may induce selection bias when parental age at birth is included in the specification. Given that the birth order findings are at the heart of the paper, I am a bit concerned that data issues may make it difficult to reliably estimate birth order effects.
Yup, though selection bias is an issue anyway. What could deceased parents do? Presumably pushes our sample to be younger. Could we compare deceased to non-deceased?
- It is good that the authors do some robustness checking of the assumption that there is no correlation between genes and birth order. This is a nice contribution of the paper as much previous literature has suggested “optimal stopping” type models as a potential explanation for birth order effects and for why, in particular, last-born children may have particularly poor outcomes.
OK fine.
Kirkebøen, L., E. Leuven, and M. Mogstad (2021). College as a marriage market. Technical report, National Bureau of Economic Research.
This is an ambitious and well-crafted paper that analyzes a model of spousal matching in which sorting is based on both genes and social status (social-genetic assortative mating, SGAM). The paper also provides some evidence that first-born siblings have spouses with higher polygenic scores for educational attainment. The technical execution seems excellent and the writing is clear and concise. I recognize that there is value in injecting tools and concepts from the genetics literature into the economics mainstream. The authors deserve credit for taking important steps in this direction. I think efforts to incorporate insights from genetics will ultimately advance our understanding of fundamental questions in economics, e.g. about the relationship between assortative mating and inequality or intergenerational transmission. On the negative side, I suspect the authors are overstating the novelty of their theory, perhaps due to lack of familiarity with the literature. At minimum, the paper needs a much more comprehensive discussion of how the modeling approach is related to an earlier literature that the current draft does not engage with in any serious way. Unfortunately, the empirical work is also subject to some number of limitations, most of which are outside the author’s control, that substantially weaken my confidence in the core findings.
The paper makes a number of claims about theoretical novelty that I am frankly struggling to wrap my head around. In order to evaluate the claims, it’d be helpful to have the authors explicitly contrast their approach to the standard modeling approaches in the literature, all of which build in one way or the other on the seminal work of Fisher (1918).
The basic setup of these models, many of which are surveyed by Otto et al. (1995), strikes me as similar overall to what the authors are doing. Phenotypes are determined as a linear combination of some latent variables. For example, a common approach is to allow three such latent variables: a genotype (G), a common-environmental (or cultural variable, C) and an environmental variable (E). The difference between C and E is that only the former is assumed to be transmissible across generations (there are many ways to model this transmission). Genotypes are transmitted across generations, following processes specified to ensure alignment with Mendelian principles.
Right, we'd better incorporate these into the lit review.... XXX
Finally, the models can accommodate a rich variety of deviations from random mating. If we denote the vector of father’s component vector Yf = (Gf,Cf,Ef) and mother’s by Ym =(Gm,Cm,Em) then they all boil down to assuming that Yf and Ym are independent conditional on some set of covariates. In principle, the covariates can be anything, including elements from the component vector of an entirely different phenotype. In practice, the most common approaches are known as phenotypic assortment and social homogamy. The main reason justification for relying on one of these assortment schemes is not that nobody had thought to consider something richer. Rather, it is that, until recently, identifying the parameters of models with richer assortment processes was simply hopeless. The availability of GWAS data has changed that.
Under phenotypic assortment, any correlation between some element of Yf and some element of Ym is assumed to disappear if we condition on the parental phenotypes themselves. Under social homogamy, the key assumption is instead that the latent variables of the mates are independent conditional on the mates’ cultural values (where cultural value should be interpreted quite broadly, and could refer to shared membership in a group of a particular status/attractiveness). Contrary to what the authors seem to imply, the idea that you could have assortment both on phenotype and social homogamy has been around for quite some time. Such so-called mixed homogamy models (e.g. Rao, Morton, and Cloninger 1979) seem similar in many ways to this paper’s theoretical approach. The models generally don’t restrict the spousal correlation between one mate’s C and the other’s G to be zero, nor do they rule out gene-environment covariance within an individual (people with high values of C tend to have higher values of G, etc). Roy, Newton, Morton and Yee (1976) formulated a model in which marriage is assortative on the basis of socioeconomic status and genotype (which seems similar to what the authors are proposing).
Esp this paper, also the Rao paper would be a good start.
If the theory developed in this paper represents a major conceptual advance relative to the earlier work, e.g. because the theory identifies some important mechanism that the earlier models do not allow for – then it needs to be clarified exactly how. Until that has been done, my suspicion that the claims are overstated will continue to linger. Doing more to harmonize the notation with earlier work would go some way toward clarifying connections. But it is not just the treatment of assortative mating relative to the previous literature that requires some more discussion. The idea that transmission parameters may differ for men and women has been around for a while (Cloninger, Rice, and Reich 1979) and it seems appropriate to acknowledge this when discussing this particular extension.
This is about a transmission parameter (e.g. mothers transmit more culture than fathers) but not about different attractiveness for males and females.
The authors point out a number of limitations of models with random mating. My general reaction is that most of these limitations are already well-known. Thanks to proliferation of GWAS data, there is already overwhelming evidence that the simplest models, which rule out gene-environment covariance within and across spouses, are simply empirically inadequate, at least for outcomes such as education. GWAS was transformational because it suddenly became possible to observe reasonable proxies for the Gs of various phenotypes. A decade ago, we simply had no way of credibly estimating the correlation between someone’s G and some feature of their environment. The principal barrier to progress was the paucity of data, not poorly developed theory (though better theory is of course welcome too).
Consider carefully what we say about why the results matter. Though here, we can stress our research design & empirics.
Esp consider what we should say about the "simple models"
The empirical work is creative, clearly described and presented. I am sorry to say I am not convinced that it moves the literature forward quite as much as the authors seem to believe. There are a number of issues that, considered together, somewhat weaken my confidence in the findings. To the authors’ credit, many of the issues are acknowledged prominently.
- There are no family fixed effects in the preferred specification. Since the parameter estimate only looks marginally significant in the specification without the FEs, I am not optimistic that the results would have held up in a within-family analyses. In addition, the authors had many investigator-degrees of freedom in specifying the analysis, choosing the estimation sample, etc. For these reasons, I think the evidence presented is only suggestive.
Sigh. Researcher degrees of freedom. All we can really do is point at github. But y'know, maybe we only put our final specification on github...
- My understanding is that enormous samples are required to reliably detect order effects for outcomes such as IQ. That makes me wonder if the analysis was well-powered to detect effects on a noisy proxy for a spousal PGI in the UKB subsample of spouses.
I don't think this is nec true and indeed we see quite large effects. Possibly controlling for parental age helps? Discussing the lit on birth order effects will help here maybe.
DONE - some bits for Oana to do
- It is unclear to me how the empirical exercise maps to the SGAM theory. What is it that SGAM predicts that other theories don’t and why? Or is SGAM being compared to a random-mating baseline?
Right.
- Conceptually, the analyses are based on the wrong PGS. In an ideal world, we would use population parameters of a within-family GWAS to construct the PGS. In practice, we have to make do with noisy estimates of a different parameter vector. The estimation error can be dealt with using standard measurement-error-correction, but it is harder to convincingly address the problem that we don’t have weights from the right type of training data (yet!).
Points we can make here: (1) v high correlation with the within-family score; (2) SNP summary statistics estimated without using UKBB, so in different countries, reducing chance of social stratification as a confound; (3) control for 100+ PCS, further reducing social stratification; anything else?
Cloninger, C. R., J. Rice, and T. Reich. 1979. “Multifactorial Inheritance with Cultural Transmission and Assortative Mating. II. A General Model of Combined Polygenic and Cultural Inheritance.” American Journal of Human Genetics 31 (2): 176–98.
Fisher, Ronald Aylmer. 1918. “The Correlation between Relatives on the Supposition of Mendelian Inheritance.” Transactions of the Royal Society of Edinburgh 52: 399–433.
Otto, Sarah P, Freddy B Christiansen, and Marcus W Feldman. 1995. “Genetic and Cultural Inheritance of Continuous Traits, Morrison Institute for Population and Resource Studies Working Paper No 64.”
Rao, D. C., N. E. Morton, and C. R. Cloninger. 1979. “Path Analysis under Generalized Assortative Mating. I. Theory.” Genetics Research 33 (2): 175–78.
Empirically the paper looks at potential genetic-social interactions in marriage, and the effects of these interactions on social mobility rates, using UK Biobank Data, a study of about 500,000 individuals born between 1935 and 1970, with both genotypes and measures of social outcomes.
The authors identify a random shock to social status, birth order, where smaller is better in terms of the phenotype. They then show that children low in birth order match to marital partners with a higher genetic predictor of years of education. But there is also a large theoretical section which builds a model of socio-genetic matching and inheritance.
Is this a significant result? I think almost everyone, even among genetic reductionists, believes that genetic assortment in marriage is based on the phenotype. Genetic assortment for educational potential is surprisingly strong given how weak matching on social phenotypes is. But we expect that potential spouses have much better measures of the educational phenotype of their potential partner than the standard “years of education.” In that case we would expect that anything, such as birth order, which changed the phenotype would result in a match to a higher genotype value spouse. So I think the paper needs clarification on what the value added of the empirical exercise is?
Need to focus on the implications a bit more I tink, maybe in the last para of the intro: not just "what's new" but also why this has large implications for e.g. transmission of inequality. But we've tried that already....
Formal Model. I appreciate the attempt to model a process - social-genetic assortative mating (SGAM) – that combines genetic and social transmission of social attributes. However, the model as described seems to assume direct matching on genotypes as well as phenotypes. That seems a very bold assumption. How do you justify that? Also if you could demonstrate with your UK Biobank data consistency with matching both on genotypes and phenotypes, then that would answer the question of the significance of the empirical demonstration. But I do not see any such demonstration in your tables.
No, that's not correct. We just don't measure all the phenotypes via which matching takes place. Clarify with a footnote or discussion.
Could Pierre think about what happens if there's noise in the matching?
Birth order and social outcomes. Table 1 in the paper shows remarkably strong birth order effects on social outcomes in the sample used by the authors (p. 23). For example, as we go from child 1 to 6: height declines by 3.5 cm, chance of university attendance declines by 40%, salary declines by about 20% of the average, Fluid IQ drops by 1.35 points on a 13 point scale.
The authors note: It is known that earlier-born children receive more parental care and have better life outcomes, including measures of SES such as educational attainment and occupational status (Lindahl 2008; Booth and Kee 2009; Black, Devereux, and Salvanes 2011).
However, if we are to consider how generalizable these results are note:
(1) Many other birth order studies find much smaller, or no effects at all. Thus Olneck and Bill (1979), in a study of brothers in the USA born 1928-50 found no significant birth order effects on educational ability, years of education, occupational status, or earnings. “The results consistently suggest that apparent birth order effects are small, spuriously inflated by the effects of family size, and statistically insignificant within families.” Similarly Daniel Kessler (1991) notes “Few empirical studies find a statistically significant influence of an individual’s birth order on her future achievement.” (p. 424) So the authors need to do more to convince that their results are in any sense generalizable. Is there a consensus on general birth order effects of the magnitudes found here?
I think we can argue that more recent findings are definitive. We can also compare our effect sizes to the literature.
DONE, and these are indeed large.
Olneck, Michael R., and Bills, David B. "Family Configuration and Achievement: Effect of Birth Order and Family Size in a Sample of Brothers." Social Psychology Quarterly 42 (1979): 135-48.
Kessler, Daniel. “Birth Order, Family Size, and Achievement: Family Structure and Wage Determination.” Journal of Labor Economics 9, no. 4 (1991): 413–26. http://www.jstor.org/stable/2535077.
(2) I have access to data for siblings born in England 1910-2000 on their adult social outcomes 1999-2021 (log house value, index of multiple deprivation for their neighborhood, are they a company director). For each measure there is no effect of birth order within families on social outcomes. Thus for log house value (lhv)
[see paper]
Don't see any control for parental age here so I think we can ignore.
Social Accidents and Assortment on the Genotype. At the core of the paper is an attempt to show that social accidents, such as birth order, influence assortment by genotype, and thus contribute to child outcomes.
Table 2 is the key here, where the authors show a direct link between birth order and spouse genotype score (PSEA). The estimated effect of birth order, relative to own PSEA, is very large.
However, despite the very large effects of birth order on the phenotype, and the large numbers of observations (10,206), birth order has marginal statistical significance. I am sorry, but years of work reading empirical papers makes me very wary of any paper which has at its core an empirical result so weakly supported. There are just so many data handling decisions made by authors that can influence the t-statistic.
This particularly shows up in the robustness section (pp. 49-59). In tables 6, 9, and 10 the results are no longer statistically significant. In what sense is that a successful robustness check?
Can you do anything to give the reader more confidence in the validity of the table 2 results?
Need to strengthen this section; maybe discuss data handling.
Table 10 indeed insignificant. Table 9, no, significant at 5%. Table 6 insignificant but this is without the parental age controls. And in all these places the pattern of the results is the same.
DONE - pushed robustness of basic result and mentioned github.