Highly educated people tend to be healthier and have higher incomes than those with less schooling. This might be because education helps people adopt a healthier lifestyle, as well as qualifying them for better-paid jobs. But, on average, highly educated people also score more highly on cognitive tests. This may explain why they tend to adopt healthier behaviours, such as being less likely to smoke. Because education and intelligence are so closely related, it is difficult to tease apart their roles in people’s health.

Davies et al. have now turned to genetics to explore this question, focusing on genetic variation associated with intelligence and education levels. Analysing genetic and lifestyle data from almost 140,000 healthy middle-aged volunteers from the UK Biobank study suggested that together, intelligence and education influence many life outcomes, but also that they have independent effects. For instance, there is evidence that more intelligent people tend to earn more, irrespective of their education. However, more educated people also tend to earn more, even after accounting for their intelligence. They also tend to have lower BMIs, be less likely to smoke, and engage in less sedentary behaviour and more frequent vigorous exercise in midlife. For each of these outcomes, the effects of education are all in addition to the effects of intelligence.

Education and intelligence thus affect life outcomes together and independently. Overall, the results of Davies et al. suggest that extending education, for example by increasing school-leaving age, could make the population as a whole healthier. However, the individuals in the current study grew up when smoking was far more common than it is today. Some of the observed effects on health may thus be due to differences in smoking rates between groups with different levels of education. If so, increasing education may not have as much impact today as it did in the past. It is also possible that these findings reflect the effects of the family environment, for example how parents influence their offspring. Larger studies are needed to investigate this hypothesis.

Intelligence and educational attainment are associated with many socioeconomic and health outcomes (Cutler and Lleras-Muney, 2006; Clark and Royer, 2013; Deary and Johnson, 2010; Deary, 2012; Hill et al., 2016a). However, the causal relationships between intelligence, education, and health outcomes are unclear, in part, because intelligence and education are strongly correlated. On average, children who score more highly in intelligence tests tend to remain in school for longer, (Deary et al., 2007) and people who remained in school for longer tend to have higher intelligence later in life (Ritchie and Tucker-Drob, 2018). Intelligence and educational attainment are partially heritable, and strongly genetically correlated (r_g=0.70) (Lee et al., 2018; Hill et al., 2019; Hill et al., 2016b; Hill et al., 2018). A review of the effects of educational attainment on socio-economic and health outcomes in later life found some evidence that increases in education led to lower mortality, especially for older cohorts (Galama et al., 2018). However, there was little consistent evidence of effects on other outcomes such as obesity (Galama et al., 2018). A systematic review of 28 studies provided evidence using quasi-experiential designs that each year of education causes measured IQ to increase by on average 1 to 5 points (Ritchie and Tucker-Drob, 2018). Large prospective studies have found that intelligence test scores taken at age 11 strongly associate with educational attainment later in life, a link that is, in part, explained by shared genetic effects (Deary et al., 2007; Calvin et al., 2012). However, there are no quasi-experimental studies of the effects of intelligence on education because intelligence is less subject to perturbation by natural experiments such as policy reforms. In order to design successful interventions aimed at the amelioration of health conditions, it is necessary to determine the extent to which intelligence, education, or both, are causal factors for health outcomes. If the health differences are mainly due to differences in intelligence that are independent from education, then changes to the length of schooling are unlikely to affect population health. If, however, educational attainment has a causal effect on health and socioeconomic outcomes later in life, and these effects are independent of intelligence, the health of the population may be able to be raised by implementing a policy change aimed at increasing the duration of education (Deary and Johnson, 2010).

Mendelian randomization is an approach that can provide evidence about the relative causal effects of intelligence and education on social and health outcomes under specific assumptions (Davey Smith and Ebrahim, 2003; Davies et al., 2018a). Mendelian randomization generally uses single nucleotide polymorphisms (SNPs) that associate with traits of interest, in this case intelligence and educational attainment, as proxy variables for a trait. At each SNP, offspring inherit at random one of their mother’s two possible alleles and one of their father’s two possible alleles. With the exception of somatic mutation, SNPs are invariant post-conception, so it is not possible for the environment or developing disease to affect inherited DNA. Thus, SNPs are not affected by reverse causation, which can distort causal interpretations of observational epidemiological associations. Segregation of alleles at germ cell formation (Mendel’s first law) and the independent assortment of alleles with respect to the rest of the genome excepting proximal DNA segments (Mendel’s second law), and the lack of environmentally influenced effects on survival from conception through to live birth and study entry, leads to genetic variants being largely unrelated to factors that would confound conventional observational studies (Davey Smith, 2011).

Instrumental variable interpretations of Mendelian randomization analysis depend on three assumptions, (1) the genetic variants associate with the risk factors of interest, (2) the genetic variants-outcome associations are not confounded by potentially unmeasured factors, and (3) the genetic variants only affect the outcomes via their effect on the exposures of interest (in this case intelligence or education) (Davies et al., 2018a). One approach would be to estimate the effects of intelligence and education separately using SNPs identified in GWAS for intelligence or education (Hill et al., 2019; Okbay et al., 2016). However, this could be misleading, as SNPs that affect intelligence are likely to also affect education and vice versa. Thus, the SNPs associated with intelligence and education are pleiotropic – and most affect both traits. However, it is unclear whether any effects of the SNPs on the health and socioeconomic outcomes later in life via education and intelligence are vertically or horizontally pleiotropic (Davey Smith and Hemani, 2014).

Consider a Mendelian randomization study with one exposure - education. Vertically pleiotropic effects would occur if the SNPs being used as proxies for education affect the outcomes first via their effects on intelligence, which then has a downstream effect on educational attainment (Figure 1a). Horizontally pleiotropic effects could occur if a SNP being used as a proxy for education directly affected an outcome via intelligence without being mediated via education (Figure 1b). In a Mendelian randomization analysis using education as a single exposure, this horizontal pleiotropy would violate the third Mendelian randomization assumption. Alternatively, the SNPs being used as proxies for education could affect intelligence, and consequently educational attainment, but all of the effects of the SNPs on the outcome could be mediated via intelligence (Figure 1c). Pleiotropy would have similar consequences for a Mendelian randomization study with intelligence as a single exposure. One method which can provide evidence about which of these scenarios is most likely is multivariable Mendelian randomization (Sanderson et al., 2018; Burgess et al., 2015). This approach simultaneously estimates the effects of two or more risk factors using a potentially overlapping set of SNPs. Multivariable Mendelian randomization estimates the direct effect of each risk factor – i.e. the direct effect of intelligence on outcomes that is not mediated via the effect of intelligence on education, and the direct effect of education that is not mediated via the effect of education on intelligence (Figure 2). It is important to note that multivariable Mendelian randomization does not overcome bias due to horizontally pleiotropic effects via other mechanisms, for example, effects via character or personality.

Figure 1

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Figure 2

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Here, we used a large sample from the UK Biobank and SNPs associated with intelligence and education to estimate the direct effects of intelligence and education on a range of health and socioeconomic outcomes. Our primary analysis uses two-sample multivariable Mendelian randomization of the effects of intelligence and education on a range of socioeconomic and health outcomes. This approach makes most efficient use of available data. We present single sample Mendelian randomization analysis using polygenic risk scores in the UK Biobank as sensitivity analyses.

The characteristics of 138,670 participants of UK Biobank who met our quality control and inclusion criteria for our primary two-sample multivariable analysis are described in Table 1. We take estimates of the SNP-intelligence and SNP-education associations from published GWAS of intelligence and education (Hill et al. and Okbay et al.) and estimates of the SNP- outcome associations using participants of the UK Biobank who were not included in either GWAS. The intelligence and education GWAS used overlapping samples, but do not overlap with the sample used to estimate the SNP-outcome associations. See Supplementary file 1 - Figure 1 for a flow chart of participants’ inclusion and exclusion into the analytic samples. The sample was 45.5% male and on average were 57.3 years old when they visited the assessment centre. The prevalence of the clinical outcomes in this sample ranged from 1.5% for stroke to 34.6% for a broad measure of depression. Of the participants in this sample, 2.0% died by the end of linked data follow-up. A total of 45.2% of the sample had ever smoked, and 9.2% were current smokers.

Bidirectional Mendelian randomization of intelligence and education

We investigated the direction of causation between intelligence and education using bidirectional two-sample Mendelian randomization. We restricted analysis to SNPs that were available in the Hill et al. (2019) intelligence genome-wide association study (GWAS), the discovery sample of Okbay et al. (2016) educational attainment GWAS, and the UK Biobank Haplotype Reference Consortium panel (HRC). We selected all SNPs that were associated with intelligence at p<5 × 10⁻⁰⁸. Of these SNPs, we then selected the lead SNPs within each 10,000 kb genomic region by selecting the SNP with the lowest p-value. We then repeated this process to select all SNPs that associated with education at p<5 × 10⁻⁰⁸, and selected lead SNPs within each region. This resulted in 270 SNPs that were associated with either intelligence or education, or both. Some of these SNPs represented the same signal, so we clumped a combined list of SNPs by selecting the SNP with the lowest p-value for education. This resulted in 219 SNPs, of which 144 were associated with intelligence, but not education at p<5 × 10⁻⁰⁸, 38 were associated with education, but not intelligence at p<5 × 10⁻⁰⁸, and 37 were associated with both intelligence and education at p<5 × 10⁻⁰⁸. All 219 SNPs associated with either trait were included in the multivariable Mendelian randomization analysis for both intelligence and education (for a flow chart of selection of SNPs see Supplementary file 1 - Figure 2).

We estimated the effects of intelligence on education and vice versa using non-overlapping data from the UK Biobank. We used two-sample summary data Mendelian randomization methods including the inverse variance weighted (IVW), MR-Egger, weighted median and modal estimators, see methods for details (Bowden et al., 2016a; Bowden et al., 2016a; Hartwig et al., 2017). The inverse variance weighted (IVW) estimates implied that a one standard deviation (SD) increase in intelligence increased years of education by 0.52 SD (95% CI: 0.48 to 0.56, p-value=2.2 × 10⁻¹⁴⁵). The IVW estimates imply that a one SD increase in education increased intelligence by 0.77 SD (95% CI: 0.68 to 0.86, p-value=3.0 × 10⁻⁶²). There was more evidence of heterogeneity in the estimated effects of education across the SNPs (I² = 0.60, 95% CI: 0.48 to 0.69) than in the estimated effects of intelligence (I² = 0.48, 95% CI: 0.38 to 0.56). The heterogeneity statistic indicates the variability of the estimated effects between SNPs; a value of zero indicates no heterogeneity and one indicates high heterogeneity. One explanation for this heterogeneity across SNPs is if the SNPs have horizontally pleiotropic effects. The effects of each of the SNPs on intelligence and education, along with the IVW, MR-Egger, weighted median and weighted mode estimates are presented in Figure 3 and Supplementary file 1 - Table 1 and 2. The estimated effect of intelligence was consistent and robust across four different estimators (IVW, MR-Egger, weighted median and weighted mode). The estimated effect of education was robust across IVW, weighted median and weighted mode, but the MR-Egger estimate was attenuated by over half, one explanation for this is if the education SNPs have unbalanced horizontally pleiotropic effects on intelligence or the INSiDE assumption is violated. There was little statistical evidence that the estimated effects of intelligence on education were biased by horizontal pleiotropy (MR-Egger intercept = 0.001, 95% CI: −0.005 to 0.003, p-value=0.68). However, these tests for pleiotropy are likely to have low power. There was modest evidence that the estimated effects of education on intelligence were affected by horizontal pleiotropy (MR-Egger intercept = 0.009, 95% CI: 0.001 to 0.016, p-value=0.03).

Figure 3

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Multivariable Mendelian randomization

Next, we estimated the direct effect of each exposure using multivariable Mendelian randomization (Sanderson et al., 2018). The direct effect of intelligence (or, mutatis mutandis, education) is the effect of intelligence that is not mediated via education (or intelligence). Multivariable Mendelian randomization estimates the effects of two exposures using the two sets of (overlapping) SNPs as instruments. We restricted the analysis to SNPs in linkage equilibrium which were identified in the intelligence and/or education GWAS at p<5 × 10⁻⁰⁸ clumped on r2 = 0.01 within 10,000 kb using the 1000 genomes reference panel (Hemani et al., 2018). Some SNPs that were selected from the intelligence and education GWAS were closely positioned in the genome and were correlated. For these pairs of SNPs, we selected the SNP that most strongly associated with education in the GWAS. Sensitivity analysis which clumped SNPs using their association in the intelligence GWAS is presented in the supplementary materials; however, the results were virtually identical. The instruments strongly predicted both education and intelligence in the single sample analysis (the minimum Sanderson-Windmeijer multivariable F-statistic was 21.6) (Sanderson et al., 2018; Sanderson and Windmeijer, 2015). Sanderson-Windmeijer F-statistics tests the strength of the SNP-exposure conditional on the other exposure (intelligence or education). Because the effects of the SNPs on intelligence and education are similar (but not identical), the Sanderson-Windmeijer multivariable F-statistics are smaller than standard univariable F-statistics. The estimates of the direct effects presented in Figure 4 are less precise than the estimates of the total effects. It is not possible to test the strength of the instruments to jointly predict both of the exposures for the two-sample analysis. However, the Sanderson-Windmeijer tests of the strength of the instruments in the single sample analysis is likely to provide a lower bound of their strength.

Figure 4

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Education and intelligence are strongly phenotypically and genetically correlated and are associated with many outcomes across the life course. However, the direction of causation underlying these relationships is not clear, and nor is the direction of association between intelligence and education. In this study, we used univariate and multivariable Mendelian randomization to estimate the total and direct effects of both years of education and intelligence on health and social outcomes. We used SNPs associated with intelligence or education, or both, at p<5 × 10⁻⁰⁸ to estimate the total and direct effects on a range of outcomes. The estimated total effects of intelligence indicate the overall effects including effects of intelligence mediated via education. The estimated total effects of education indicate the overall effects of education including the effects mediated via intelligence. Whereas the direct effects of intelligence are those that are not mediated via education, and the direct effects of education are those that are not mediated via intelligence. Multivariable Mendelian randomization does not overcome bias due to other pleiotropic effects by pathways other than intelligence or education. Both intelligence and educational attainment had beneficial total effects on most outcomes (the exception being alcohol consumption). Intelligence had positive direct effects on income and alcohol consumption, and negative direct effects on moderate and vigorous physical activity. Education had positive direct effects on household income, BMI, alcohol consumption, and rates of vigorous physical activity, and negative direct effects on sedentary behaviour. These estimates suggest that both intelligence and education affect a range of socioeconomic and health-related outcomes. Many of the direct effects for both traits were substantially attenuated compared to the total effects. For example, the direct effects of intelligence on income were 54% to 89% smaller than the total effect. The direct effects of education were 27% to 38% smaller than the total effects.

Previous studies have demonstrated that both intelligence and education positively associate with health and longevity (Hill et al., 2019; Batty et al., 2007; Gottfredson and Deary, 2004; Plomin and Deary, 2015; Davey Smith et al., 1998). A systematic review of cohort studies found people who had a one standard deviation higher childhood intelligence had 24% (95%CI: 23% to 25%) lower mortality across between 17 and 69 years of follow-up (Calvin et al., 2011). In contrast, using molecular genetic data we found little evidence of a large effect of intelligence on mortality. This inconsistency may be because this sample of the UK Biobank was only followed-up for an average of 7.8 years, limiting our power to detect an effect on a relatively rare outcome (<2%), or because of selection bias. A large literature has investigated the associations of education and mortality and morbidity. For example, Galama et al., 2018 reviewed studies which had used RCTs and natural experiments to estimate the effect of education on mortality, obesity and smoking (Galama et al., 2018). They found that estimates of the effect of educational attainment were heterogenous. Our results suggest that education has a larger direct effect on ever or current smoking. We found some evidence of a direct effect of education, but not intelligence, on BMI. The difference between our study and the studies reviewed in Galama et al. may be that we used a continuous rather than binary measure of adiposity. However, we still found evidence that education affected rates of overweight (67% prevalence) and obesity (24% prevalence) using the individual participant data analysis reported in Supplementary file 1 - Figure 4. Gathmann et al. (2015) reviewed the effect of 18 school reforms across Europe on mortality (Gathmann et al., 2015). They estimated that an additional year of schooling reduced male mortality over 20 and 30 years by 1.7% (95%CI: 0.2% to 3.2%) and 3.9% (95%CI: 1.8% to 6.0%). They report weak evidence that the effects on female mortality were smaller (0.9%, 95% CI: −1.2 to 2.9% and 1.8%, 95% CI: −0.1 to 3.6% reductions at 20 and 30 years respectively, p-value for difference by gender = 0.27 and 0.07). Hamad et al. (2018) systematically reviewed the literature using quasi-experimental methods to estimate the effects of education. They included 89 studies, and found that education had small beneficial effects on mortality, smoking and obesity (Hamad et al., 2018). Our results using genetic data for mortality were imprecise as the number of deaths to date has been relatively low. Over time as the number of deaths increase there will be more precision to investigate this hypothesis in the UK Biobank.

Researchers using univariable Mendelian randomization have found that education generally reduces risk of a range of outcomes (Tillmann et al., 2017). Larson et al. used two-sample Mendelian randomization and found that higher educational attainment reduced the risk of Alzheimer’s disease. (Larsson et al., 2017) Potential explanations for these apparent protective effects of education on later health outcomes are: that they were due to (1) vertically pleiotropic effects of SNPs via intelligence and subsequently education (Figure 1a), (2) horizontally pleiotropic effects of the SNPs via intelligence (Figure 1b), and (3) confounding pleiotropic effects of the SNPs where the SNPs affect intelligence and education, but only intelligence affects the outcomes (Figure 1c). The total effects of intelligence and education on income had a similar direction. There was evidence of a total effect of education, but little evidence of a total effect of intelligence on many measures of morbidity and mortality and BMI (Supplementary file 1 - Table 3). The direct effects of education and intelligence, estimated by multivariable Mendelian randomization, were smaller than the total effects. The direct effects of intelligence were generally smaller than the direct effects of education (Figure 4). One explanation for this is that the SNPs have vertically pleiotropic effects via intelligence and education on the outcomes. The non-zero direct effects of education suggest that the effects of education estimated by univariable Mendelian randomization are unlikely to entirely be due to horizontally pleiotropic (direct) effects on the outcomes via intelligence. In another study, we used multivariable Mendelian randomization to estimate the direct effects of intelligence and educational attainment on Alzheimer’s disease. The relationships between intelligence and education and Alzheimer’s disease was largely due to an effect of intelligence (Anderson et al., 2018).

As with all analytic methods, inferences using multivariable Mendelian randomization depend on assumptions. Specifically: (1) the SNPs associate with intelligence even after conditioning on education and vice versa, (2) there are no confounders of the SNP-outcome associations, and (3) intelligence and/or education mediate all of the effects of the SNPs on the outcome (i.e. no horizontal pleiotropy mediated via factors other than intelligence or education). The first assumption is stronger than required for univariable Mendelian randomization (Sanderson et al., 2018). In the single sample setting, this can be tested using the Sanderson-Windmeijer test (Sanderson and Windmeijer, 2015). The SNPs exceed the critical values for this test for each exposure (Supplementary file 1 - Table 4) and the results are unlikely to suffer from weak instrument bias. It is not possible to prove the second assumption (independence) holds, because some confounders may be unmeasured or remain unknown.

This study investigated one of the most likely horizontally pleiotropic mechanisms in a univariable Mendelian randomization analysis of the effect of education on outcomes later in life: intelligence. SNPs which associate with intelligence in GWAS also strongly associate with education (Okbay et al., 2016). Indeed it would be surprising if there were SNPs that associated with intelligence that did not influence education. However, are these associations due to horizontal or vertical pleiotropy? Vertical pleiotropy would imply that the SNPs’ effects on the outcomes are via an effect on intelligence and subsequently education. Horizontal pleiotropy would mean that the SNPs have direct effects on the outcomes via intelligence which are not mediated via an effect on education (Figure 2). Multivariable Mendelian randomization estimates of the direct effects of intelligence and education on the outcomes. Thus, they allow for any horizontal or vertical pleiotropic effects via intelligence or education. The estimated direct effects of intelligence on smoking, household income, BMI, alcohol consumption and sedentary behaviour were substantially attenuated compared to the total effects (Supplementary file 1 - Figure 3). This attenuation suggests that a substantial fraction of the total effects of intelligence on the outcomes were mediated via education.

What are the policy implications of these results? Economists and policymakers have been interested in the consequences of education for outcomes later in life. The length of education has increased in many countries around the world. If education affects later health and social outcomes, then this may result in improvements in public health. Our results suggest that education is likely to affect health, although these effects are smaller than indicated by a naïve Mendelian randomization analysis that assumes the SNPs have no horizontally pleiotropic effects via intelligence. Each additional year of education (0.19 SD in UK Biobank) would result in a 2.0pp, 3.1pp, 2.4pp, 1.0pp increase in probability of having household income above £18 k, £31 k, £52 k and £100 k respectively, a 0.04 units increase in alcohol consumption (on a 1 to 5 Likert scale), 8.87 fewer minutes of sedentary behaviour per day, and 0.06 more days vigorous activity per week.

All code used to produce the results in this study will be uploaded to GitHub (https://github.com/nmdavies/ukbiobank-intell-vs-ea; copy archived at https://github.com/elifesciences-publications/ukbiobank-intell-vs-ea). All data used in this study will be archived with the UK Biobank. Researchers who obtain the relevant permissions from the UK Biobank data access committee will be able to access the dataset (http://biobank.ndph.ox.ac.uk/crystal/dset.cgi?id=1762).

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Thank you for submitting your article "The effects of intelligence and education on health, a bidirectional two-sample Mendelian randomization analysis" for consideration by eLife. Your article has been reviewed by two peer reviewers, and the evaluation has been overseen by a Reviewing Editor and Eduardo Franco as the Senior Editor. The following individual involved in review of your submission has agreed to reveal his identity: Stephen Burgess (Reviewer #1).

The reviewers have discussed the reviews with one another and the Reviewing Editor has drafted this decision to help you prepare a revised submission.

Summary:

This paper consists of a series of Mendelian Randomization (MR) studies related to intelligence, education, and later-life outcomes attempting to disentangle the complicated relationship between them. The analyses included in this study appear to be comprehensive, using many of the latest tools that have been developed. The choice of methods is generally appropriate, and the presentation of results is clear and measured. This work is interesting, and a great example of the potential of the multivariable MR approach to disentangle the effects of related risk factors. However, we have major concerns regarding the extensive use of causal language as there is some evidence that the key assumptions of MR may not hold in this application.

Essential revisions:

1) It is appreciated that the authors include the assumptions required for univariate and multivariate MR and the discussion of the limitations. However, the discussion of these assumptions and limitations need to be more complete and more central in the paper. MR analyses live or die to the degree that they satisfy the assumptions of the method. When this entire discussion is added to a section at the very end of the paper, it makes it very difficult as a reader to assess the credibility of the evidence being presented. Some further formal evaluation of whether assumptions hold could be presented. If the genetic risk score is as associated with confounders (notably socio-economic) as education itself, then the benefit of MR is less clear. (Note some association with confounders is expected, as education itself will influence socio-economic variables somewhat.) Perhaps a comparison with parental socio-economics would be helpful here – genetic variants should be less associated with parental socio-economics (if the MR assumptions are satisfied).

2) Related to the above point, the causal language throughout the paper is too strong. For example, in the limitations section, the authors acknowledge that dynastic effects and assortative mating could be driving "some of the effects [they] report." Indeed, the data is consistent with a model where the nurturing environment affects health but where education and intelligence have no effect at all. Despite this, there is unqualified causal language in the title, Abstract and throughout the manuscript. This should all be greatly softened.

3) Intelligence and education are difficult to define and measure – particularly intelligence. This is an intrinsic concern of any research involving intelligence, but it is particularly relevant for research that makes causal inferences and public policy recommendations (as per the final line of the Abstract). What would it look like to increase intelligence? What aspect of intelligence would we increase? There is also a methodological concern here – while the multivariable Mendelian randomization analyses are important for understanding questions of aetiology, the univariable Mendelian randomization analyses are more important for understanding the impact of public health interventions. As most interventions to increase intelligence would do so via education. Hence the total effects of intervention on intelligence and education should be as important as the direct effects. We would therefore encourage a co-equal presentation of these results.

4) The reviewers raised concerns about the use of multivariable Mendelian randomization for two variables that are so highly correlated. This is alleviated by the reasonably healthy Sanderson-Windmeijer F statistics, but particularly when the direct effects are in opposite directions (as for several examples in Figure 4 in Supplementary file 1), we worry slightly that this is just an artifact of including two highly correlated predictors in a regression model – due to chance variation, one will end up with a positive estimate and the other with a negative estimate. Having said that, it is reassuring that this pattern doesn't hold for all the outcomes. What is the correlation between genetic associations with education and genetic associations with intelligence?

5) Measurement error – while you are correct that standard univariable Mendelian randomization is not particularly influenced by measurement error, the same is not necessarily true for multivariable Mendelian randomization. As this is based on multivariable regression, it is possible for measurement error in genetic association estimates to lead to bias in any direction. It may be the case that the expected bias is low, but we are not aware of any theoretical or simulation work on this topic.

6) While we understand removing participants in the interim release for the analysis of genetic associations with intelligence/education, these participants could be included in analyses for other outcomes. We understand if you prefer to keep a consistent sample definition for comparability, but you may get improvement in power by using a wider sample for the gene-outcome associations. As a side point, in Figure 1 in Supplementary file 1, could you make clear where the two samples come from in the two-sample analyses? Currently there is only one box, but logically we'd expect there should be two.

7) It was difficult to identify the exact procedures followed in the paper at times. This was especially the case when they describe what data are used and which summary statistics are used. For example, the authors state, "The characteristics of 124,661 participants of UK Biobank who met our quality control and inclusion criteria for our primary analysis are described in Table 1." What is considered the "primary analysis" of this paper? The bidirectional EA vs. intelligence analysis, the univariate analysis, or the bivariate analyses? Or perhaps all three of them? Given that the authors also describe using published GWAS results, it is not clear how these UK Biobank participants are used. Just for the outcome phenotypes? Additionally, the descriptions of the Sanderson-Windmeijer test and the clumping procedure is ambiguous and hard to follow.

[Editors' note: further revisions were requested prior to acceptance, as described below.]

Thank you for resubmitting your work entitled "Intelligence, education and health, evidence from bidirectional two-sample Mendelian randomization" for further consideration at eLife. Your revised article has been favorably evaluated by Eduardo Franco as the Senior Editor, M Dawn Teare as the Reviewing Editor, and two reviewers.

The manuscript has been improved but there are some remaining issues that need to be addressed in a new revision round before acceptance, as outlined below:

The evidence that the IV assumptions may have been violated is rather underplayed and this needs to be more firmly acknowledged and stated within this manuscript either in the Discussion or in the limitations. One reviewer also highlights that measurement error can have an impact on Multivariable MR.

Reviewer #1:

I'm happy with how the authors have edited the paper. While the paper relies on assumptions, these are clearly laid out and considerable effort has been made to assess the assumptions.

Reviewer #2:

I appreciate the authors' substantial revisions in response to comments of the reviewers. The specific steps that were taken by the researchers is much more clear. I also appreciate the new analyses to test the assumptions of the method. I still have two substantive concerns, however.

1) While the authors describe the limitations of the methods they employ, they give a much more rosy interpretation of their sensitivity results than I think is merited. The two well-powered pieces of evidence the authors present related to the validity of the MR assumptions are the published studies on indirect effects of parents and the evidence that the polygenic scores are strongly associated with covariates related to childhood environment. Despite this, the authors make conclusions like "the impact of these associations on the final results may be small" and that "Assumption 2 [no confounders] is plausible because of the random inheritance of alleles at conception". My conclusion upon reading the analyses is that the assumptions of MR probably don't hold in this case and that the bias is potentially substantial. Do the authors disagree? If so, the authors should provide evidence for why they think this is the case or what evidence they have that the bias induced by violations of this assumptions is negligible. Otherwise, the authors should use more conservative language throughout about their sensitivity analyses and should minimally include a line in the Abstract about how they find evidence that the MR assumptions may not hold in this case.

2) I was not able to follow what was being done exactly based on the description of the bias component plots in the last paragraph of the subsection “Sensitivity analysis”, subsection “Investigating bias” of the Materials and methods, and the figure legends for Figures 6 and 7 in Supplementary file 1. A description of the procedure for producing this plot should be clarified.

Essential revisions:

1) It is appreciated that the authors include the assumptions required for univariate and multivariate MR and the discussion of the limitations. However, the discussion of these assumptions and limitations need to be more complete and more central in the paper. MR analyses live or die to the degree that they satisfy the assumptions of the method. When this entire discussion is added to a section at the very end of the paper, it makes it very difficult as a reader to assess the credibility of the evidence being presented. Some further formal evaluation of whether assumptions hold could be presented. If the genetic risk score is as associated with confounders (notably socio-economic) as education itself, then the benefit of MR is less clear. (Note some association with confounders is expected, as education itself will influence socio-economic variables somewhat.) Perhaps a comparison with parental socio-economics would be helpful here – genetic variants should be less associated with parental socio-economics (if the MR assumptions are satisfied).

The vast majority of the measures in the UK Biobank indicate phenotypes in later life – there is very little information about early life conditions. For example, the UK Biobank did not include any measures of parental background. We have published quite extensively on the relationship between the education score and various confounders.

We investigated the association between the Sniekers (which is a subset of the Hill et al. data) and Okbay score and a limited number of covariates indicating the environment because we had very little power in the bivariate analysis and current bias assessment tools only allow for one exposure. The results of this analysis are shown in Supplementary file 1, Figures 6 and 7, for the Sniekers and Okbay scores respectively around the time of birth or early life using covariate balance plots.¹ We had to use the Sniekers rather than the Hill because the latter used UK Biobank data from the full UK Biobank release, however it should be noted that the genetic correlation between the Hill et al. data and the Sniekers data is rg = 1 as shown in Figure 3 of Hill et al. We have focused on the univariate analysis. We describe the methodology behind the bias plots more completely in Davies et al., 2017.¹ The bias plots estimate the relative bias caused by omitting a specific component from either the multivariable adjusted regression analysis or the instrumental variable Mendelian randomization analysis. These estimates adjust for the same set of covariates as the main analysis (PCs, sex, age, sex*age interactions). They account for the fact that a given association with a covariate will result in a much bigger bias in an instrumental variable analysis because the instrumental variable analysis only uses a small proportion of the variation in the exposure. What the plots show is that there is some evidence that on average individuals born in the south of the United Kingdom, those born in less deprived areas, or those born closer to London have higher values of the Sniekers allele score. However, the bias estimates for Index of Multiple Deprivation (IMD) are very similar for both the score and the intelligence measure in UK Biobank. Participants whose mother did not smoke in pregnancy were likely to have higher values of the Sniekers allele score. There was little evidence of associations with the other covariates. This is fairly modest evidence of bias. The education score was associated with the measures of geography, there was evidence it associated with measures of early life experience, such as breastfeeding.

How should these plots be interpreted?

There were similar associations with number of siblings as with measured education. These plots indicate that the education score does associate with early life socioeconomic measures. However, the extent of bias caused by these associations is unclear. The total bias caused by any of these potential confounders is the product of the association of the covariate with the score and the association with the outcome. We can get an indication of the total bias induced in the effect estimates by running a sensitivity analysis adjusting for these variables. Note these variables have missing values, which reduces the overall sample size and power. We reran the individual participant data additionally adjusting for these covariates and present the results in Figure 5 in Supplementary file 1. As a result of the missing values there are fewer observations and wider confidence intervals. However, there are few detectable differences between these adjusted results and the results presented in Figure 5 in Supplementary file 1.

Another way to control for family background is to run an analysis using sibling fixed effects. This is equivalent to running a difference model within siblings. Any factors that are invariant across siblings, e.g. ancestry or shared familial environmental factors, will be controlled for. A disadvantage of this approach is that there are only 38,000 siblings in UK Biobank and controlling for a family fixed effects substantially reduces statistical power. We found little evidence that our estimates differed across these models. However, this may reflect limited statistical power. However, the vast majority of estimates were larger than the in the within family analysis than the univariate IVW analysis. Interestingly, the implausible estimated effect of education on height attenuated entirely to the null in these models, suggesting that an effect of education in the offspring is unlikely to be driving these results. The results of this analysis are shown in Table 1 in Supplementary file 1. However, this analysis is underpowered. Therefore, we ideally need more data to evaluate this issue. We are in the process developing a consortium of family studies to investigate this issue with a much larger sample of siblings and trios.

We have included a new paragraph in the Results describing this analysis:

“We investigated whether the genetic variants associate with age at baseline. Without adjustment a one standard deviation increases in the Sniekers et al. and Okbay et al. scores were associated with 0.05 (95%CI: 0.0012 to 0.098, p-value=0.044) and 0.058 (95%CI: 0.020 to 0.096 p-value= 0.003) increases in age in years at baseline. […] Overall this suggests that while the there is some evidence that the scores associate with covariates, the impact of these associations on the final results may be small.”

We have included a new paragraph in the Discussion covering these sensitivity analyses:

“Mendelian randomization studies using samples of unrelated individuals can be biased by bias due to population stratification and difference in ancestry across variants and selection and participation bias (Haworth et al., 2018; Taylor et al., 2018. […] These analyses suggested that while the genetic scores for intelligence and education associate with some measures of early life experience and place of birth, the bias induced in our estimates may be limited.”

We have included a new section in the Materials and methods describing this analysis:

“Investigating bias: We used covariate balance plots to investigate whether the bias from excluding a limited set of covariates would result in more bias in the multivariable adjusted or instrumental variable analysis.¹[…] Finally, we investigated whether the results were due to the family environment by including a family fixed effect in the sample of siblings from the UK Biobank.”

2) Related to the above point, the causal language throughout the paper is too strong. For example, in the limitations section, the authors acknowledge that dynastic effects and assortative mating could be driving "some of the effects [they] report." Indeed, the data is consistent with a model where the nurturing environment affects health but where education and intelligence have no effect at all. Despite this, there is unqualified causal language in the title, Abstract and throughout the manuscript. This should all be greatly softened.

The aim of our paper is to investigate the causal effects of intelligence and education on health outcomes. All Mendelian randomization estimates are dependent on assumptions, which we define in the Introduction. In the Discussion we describe possible sources of bias. However, throughout we refer to a) total effects and b) direct casual effects.

We have edited the manuscript as suggested. We have changed the title to: “Intelligence, education and health, a bidirectional two-sample Mendelian randomization analysis”.

We have edited the Abstract to read:

“Intelligence and education are both predictive of better physical and mental health, socioeconomic position (SEP), and longevity. […] If the assumptions of Mendelian randomization hold, these findings suggest a causal relationship with intelligence and education both being potential targets for interventions aimed at improving health outcomes.”

In the Introduction we have revised the start of the second paragraph to read:

“Mendelian randomization is an approach that can provide evidence about the relative causal effects of intelligence and education on social and health outcomes under specific assumptions.”

Throughout we have revised the manuscript to refer to estimated total effects and direct causal effects.

3) Intelligence and education are difficult to define and measure – particularly intelligence. This is an intrinsic concern of any research involving intelligence, but it is particularly relevant for research that makes causal inferences and public policy recommendations (as per the final line of the Abstract). What would it look like to increase intelligence? What aspect of intelligence would we increase? There is also a methodological concern here – while the multivariable Mendelian randomization analyses are important for understanding questions of aetiology, the univariable Mendelian randomization analyses are more important for understanding the impact of public health interventions. As most interventions to increase intelligence would do so via education. Hence the total effects of intervention on intelligence and education should be as important as the direct effects. We would therefore encourage a co-equal presentation of these results.

The test used to measure intelligence in the Hill et al. data set was primarily the verbal numerical reasoning test (VNR). This test has been shown to genetically correlate at 0.81 (S.E. = 0.09, p = 6.2 X 10^-18) with a general factor of cognitive ability derived by extracting the first unrotated principal component from a battery of psychometric tests.² General factors derived from different batteries of cognitive tests have very high phenotypic correlations, often in excess of 0.95,^3,4 and are used in epidemiological studies, brain imaging studies, as well as genetic studies.⁵ As the Hill et al. intelligence phenotype is genetically highly similar to a general factor of cognitive ability, intelligence, whilst difficult to measure, has been measured in the current study in a manner consistent with that used in the literature.

As far as we are aware, with the exception of education, there are no interventions that can increase intelligence over the long term.⁶ Whether the association of education and later outcomes is due to intelligence, or education, is a key question for socioeconomic researchers – for exactly the reasons you give – the policy implications. If education associates with later outcomes because of pre-existing differences in intelligence between individuals, then policies to increase the length of schooling, or other educational interventions are unlikely to affect later outcomes. Conversely, if the effects of intelligence are mediated via schooling, then it suggests that both exposures can potentially be intervened on to affect outcomes. This study is relatively unusual because we have plausible natural experiments for both intelligence and education. While, as with all empirical analysis, these estimates depend on specific assumptions, they provide a new source of evidence about this debate. We have added the total effects to the Abstract.

4) The reviewers raised concerns about the use of multivariable Mendelian randomization for two variables that are so highly correlated. This is alleviated by the reasonably healthy Sanderson-Windmeijer F statistics, but particularly when the direct effects are in opposite directions (as for several examples in Figure 4 in Supplementary file 1), we worry slightly that this is just an artifact of including two highly correlated predictors in a regression model – due to chance variation, one will end up with a positive estimate and the other with a negative estimate. Having said that, it is reassuring that this pattern doesn't hold for all the outcomes. What is the correlation between genetic associations with education and genetic associations with intelligence?

If two exposures are very highly correlated, then multivariate Mendelian randomization will have lower power. There is a large literature on testing for weak instruments with multiple exposures, e.g. see references. This literature led to the development of multivariate weak instrument tests – such as the Sanderson-Windmeijer F-test. The null hypothesis of this test is that there is insufficient variation to identify the separate effects of the two exposures. This statistic essentially tests whether the instruments explain sufficient variation in one exposure, conditional on the other exposure.

Intelligence and education are very highly correlated – but not perfectly correlated. As a result, the F-statistic falls from 548 and 1661 for intelligence and education in the univariate case, to 27.2 and 27.4 for the multivariate Sanderson-Windmeijer F-statistic. This provides strong evidence that while there is far less statistical power for the multivariate analysis, the instruments do explain sufficient variation in the two exposures, and the analysis is unlikely to suffer from weak instrument bias.

Lee and colleagues estimated that the genome-wide genetic correlation between cognitive performance and educational attainment were genetic correlated r_g=0.662. The coefficients on intelligence and education for the SNPs included in this study were correlated to a very similar degree r_g=0.64 for the 194 SNPs selected from the Hill et al. and r_g=0.59 for the 75 SNPs selected from the Okbay et al. GWAS. Thus, while most of these SNPs affect intelligence and educational attainment in the same direction, they do not have identical effects on each trait. We use this difference in the size of effect of the SNPs on each trait to identify the effects of intelligence and educational attainment.

5) Measurement error – while you are correct that standard univariable Mendelian randomization is not particularly influenced by measurement error, the same is not necessarily true for multivariable Mendelian randomization. As this is based on multivariable regression, it is possible for measurement error in genetic association estimates to lead to bias in any direction. It may be the case that the expected bias is low, but we are not aware of any theoretical or simulation work on this topic.

Ordinary least squares (OLS) will be biased towards the null if there is random measurement error on the exposures. Random measurement error on the exposure does not affect the covariance of the outcome and the exposure. Whereas random measurement error will inflate the variance of the measured exposure relative to the true underlying exposure. These terms are the numerator and denominator of the OLS estimator, and hence if the denominator of the estimator is inflated, the OSL estimate will be downwards biased. In contrast the instrumental variable estimator is the instrument-outcome covariance divided by the instrument-exposure covariance. If the measurement error is independent of the instrument, then it will not affect the instrument-exposure covariance.

We do not know of any theoretical reason why random measurement error on the exposures would affect multivariable instrumental variable estimates. We have conducted a simple simulation to investigate this point. We found no evidence that measurement error would cause bias to a multivariable instrumental variable estimate.

We simulated three random error terms for the outcome and two exposures, and a random confounder:

v,u,e,c~N0,1.

We generated correlated instruments:

rg~N0,1

zx1=0.3*N0,1+0.7*rg

zx2=0.3*N0,1+0.7*rg

We generated the exposures:

x1=zx1+c+v

x2=zx2+c+u

We generated the outcome:

y=x1+x2+c+e

We generated two miss measured exposures. Measurement error:

me1,me2~N0,1

Miss measured variables:

x1,measured=x1+me1

x2,measured=x2+me2

We ran instrumental variable regression (2SLS) for both measured and true underlying exposures. The true exposures were unbiased (β=1.01, SE=0.007 and 0.986, SE=0.007). When two miss measured exposures were included the estimates were unbiased (β=1.01, SE=0.012 and 0.977, SE=0.012). When one exposure was miss measured, these estimates were still unbiased, but more precise than using two miss measured exposures (β=1.01, SE=0.0084 and 0.982, SE=0.0084). In these simulations, random measurement error increases the standard error of the estimates, but it does not cause bias.

We have included the code for this simulation below.

//Neil Davies 12/03/2019

//This simulates a multivariable MR study with measurement error on the exposures

clear

set obs 250000

//Generate errors

gen v=rnormal()

gen u=rnormal()

gen e=rnormal()

gen c=rnormal()

//Generate correlated instruments

gen rg=rnormal()

gen z_x1=0.3*rnormal()+0.7*rg

gen z_x2=0.3*rnormal()+0.7*rg

//Generate the exposures

gen x1=z_x1+c+v

gen x2=z_x2+c+u

//Generate the outcome

gen y=x1+x2+c+e

//Run IV regression

ivreg2 y (x1 x2 =z*),ro

//Repeat with measurement error

//Generate measurement error

gen me1=rnormal()

gen me2=rnormal()

gen x1_measured=x1+me1

gen x2_measured=x2+me1

//Run IV regression

ivreg2 y (x1_measured x2_measured =z*),ro

//Remains unbiased

//Run IV regression with one miss measured and one measured accurately variable

ivreg2 y (x1 x2_measured =z*),ro

6) While we understand removing participants in the interim release for the analysis of genetic associations with intelligence/education, these participants could be included in analyses for other outcomes. We understand if you prefer to keep a consistent sample definition for comparability, but you may get improvement in power by using a wider sample for the gene-outcome associations. As a side point, in Figure 1 in Supplementary file 1, could you make clear where the two samples come from in the two-sample analyses? Currently there is only one box, but logically we'd expect there should be two.

The interim release of the UK Biobank was included in the Hill et al. intelligence GWAS used to identify the SNPs associated with intelligence. As a result, if the outcomes of these individuals were included in the single sample analysis it could induce bias. While we acknowledge that this bias may well be small, the additional power from including these individuals in the single sample analysis is also likely to be modest. Therefore, we would prefer not to include these individuals in the single sample analysis. We excluded these individuals from the two-sample analysis for the same reason. We have added a note to Figure 1 in Supplementary file 1 that the exposure data for the two-sample analysis comes from the Hill et al. and Okbay et al. papers.

7) It was difficult to identify the exact procedures followed in the paper at times. This was especially the case when they describe what data are used and which summary statistics are used. For example, the authors state, "The characteristics of 124,661 participants of UK Biobank who met our quality control and inclusion criteria for our primary analysis are described in Table 1." What is considered the "primary analysis" of this paper? The bidirectional EA vs. intelligence analysis, the univariate analysis, or the bivariate analyses? Or perhaps all three of them? Given that the authors also describe using published GWAS results, it is not clear how these UK Biobank participants are used. Just for the outcome phenotypes? Additionally, the descriptions of the Sanderson-Windmeijer test and the clumping procedure is ambiguous and hard to follow.

The primary analysis is the two-sample multivariable Mendelian randomization of the effects of intelligence and education on the outcomes, as this is the approach that has the smallest standard errors and makes most efficient use of the available data.

We have amended the Introduction to include:

“Our primary analysis uses two-sample multivariable Mendelian randomization of the effects of intelligence and education on a range of socioeconomic and health outcomes. This approach makes most efficient use of available data. We present single sample analysis as sensitivity analyses.”

We have edited the start of the Results section to make this and the how the different samples were used clear:

“The characteristics of 124,661 participants of UK Biobank who met our quality control and inclusion criteria for our primary two-sample multivariable analysis are described in Table 1. We take estimates of the SNP-intelligence and SNP-exposure associations from published GWAS of intelligence and education (Hill et al. and Okbay et al.), and estimate the SNP-outcome associations using participants of the UK Biobank who were not included in either GWAS.”

In the Materials and methods we have clarified how the clumping was conducted:

“We restricted the analysis to SNPs in linkage equilibrium which were identified in the intelligence and/or education GWAS at p<5x10^-08 clumped on r2=0.01 within 10,000kb using the 1000 genomes reference panel.⁷[…] For these pairs of SNPs, we selected the SNP that most strongly associated with education in the GWAS.”

We have added a further explanation of the Sanderson-Windmeijer F-statistics. Essentially these are just tests of whether the SNP explains the exposure after conditioning on the other exposure:

“Sanderson-Windmeijer F-statistics tests the strength of the SNP-exposure conditional on the other exposure (intelligence or education). Because the effects of the SNPs on intelligence and education are similar (but not identical), the Sanderson-Windmeijer multivariable F-statistics are smaller than standard univariable F-statistics.”

Please let us know if there are any other aspects of the paper we can clarify.

References:

1) Davies, N. M. et al. How to compare instrumental variable and conventional regression analyses using negative controls and bias plots. Int J Epidemiol (2017). doi:10.1093/ije/dyx014

2) The neuroCHARGE Cognitive Working group et al. Molecular genetic aetiology of general cognitive function is enriched in evolutionarily conserved regions. Translational Psychiatry 6, e980–e980 (2016).

3) Johnson, W., Bouchard, T. J., Krueger, R. F., McGue, M. and Gottesman, I. I. Just one g: consistent results from three test batteries. Intelligence 32, 95–107 (2004).

4) Johnson, W., Nijenhuis, J. te and Bouchard, T. J. Still just 1 g: Consistent results from five test batteries. Intelligence 36, 81–95 (2008).

5) Deary, I. J. Intelligence. Annu Rev Psychol 63, 453–482 (2012).

6) Ritchie, S. J. and Tucker-Drob, E. M. How Much Does Education Improve Intelligence? A Meta-Analysis. Psychological Science 29, 1358–1369 (2018).

7) Hemani, G. et al. The MR-Base platform supports systematic causal inference across the human phenome. eLife 7, (2018).

[Editors' note: further revisions were requested prior to acceptance, as described below.]

Reviewer #2:

I appreciate the authors' substantial revisions in response to comments of the reviewers. The specific steps that were taken by the researchers is much more clear. I also appreciate the new analyses to test the assumptions of the method. I still have two substantive concerns, however.

1) While the authors describe the limitations of the methods they employ, they give a much more rosy interpretation of their sensitivity results than I think is merited. The two well-powered pieces of evidence the authors present related to the validity of the MR assumptions are the published studies on indirect effects of parents and the evidence that the polygenic scores are strongly associated with covariates related to childhood environment. Despite this, the authors make conclusions like "the impact of these associations on the final results may be small" and that "Assumption 2 [no confounders] is plausible because of the random inheritance of alleles at conception". My conclusion upon reading the analyses is that the assumptions of MR probably don't hold in this case and that the bias is potentially substantial. Do the authors disagree? If so, the authors should provide evidence for why they think this is the case or what evidence they have that the bias induced by violations of this assumptions is negligible. Otherwise, the authors should use more conservative language throughout about their sensitivity analyses and should minimally include a line in the Abstract about how they find evidence that the MR assumptions may not hold in this case.

There is evidence, both in our paper, and elsewhere (e.g. Kong et al., 2018, Haworth et al., 2019, Abdellaoui et al., 2018) that the education associated variants associate with family background. These associations can be induced by residual population stratification, assortative mating, and dynastic effects. However, these effects do not necessarily induce bias in Mendelian randomization estimates of the effect of education on other outcomes. The overall bias is a function of the association of the SNPs and family background, and the association of family background and the outcome. Any effect of the family background on the exposure (education) will not cause bias in the Mendelian randomization estimates. We assessed the sensitivity of our results to these sources of bias by comparing our results with and without adjustment for principal components. There was very little evidence that the effects differed. This is consistent with the principal components (which indicate geographic ancestry) not being a major confounder of the SNP-outcome associations. The second sensitivity analysis we conducted was the sibling analysis which perfectly controls for population structure, common dynastic effects, and assortative mating. Again, using this analysis we found little evidence that our estimates differed. Therefore, while the Mendelian randomization assumptions are unlikely to perfectly hold, we found little evidence that violations in these assumptions resulted in bias in our estimates. Finally, in previous papers, we have used the raising of the school leaving in 1957 to provide further evidence about the effects of education. We found consistent evidence of effects of education for a number of outcomes (Davies et al., 2018). Nevertheless, many of these sensitivity analyses are underpowered, and they are certainly insufficient to prove that the violations of the Mendelian randomization assumptions do not meaningfully affect or explain our results. We need more evidence, particularly from family studies to resolve this.

We have made the following edits:

Subsection “Limitations”: Assumption 2 is plausible because of the random inheritance of alleles at conception. It is not possible to prove the second assumption (independence) holds, because some confounders may be unmeasured or remain unknown.

Overall this suggests that while the there is some evidence that the scores associate with covariates, the impact of these associations on the final results may be small there is little evidence from these sensitivity analyses that these violations of the Mendelian randomization assumptions affects our results.

2) I was not able to follow what was being done exactly based on the description of the bias component plots in the last paragraph of the subsection “Sensitivity analysis”, subsection “Investigating bias” of the Materials and methods, and the figure legends for Figures 6 and 7 in Supplementary file 1. A description of the procedure for producing this plot should be clarified.

We have added the following sentence to the Results:

“This approach compares the omitted variable bias that occurs if a specific measured covariate is omitted from the multivariable adjusted and instrumental variable regression.”

We have added the following description to the Materials and methods:

“These tests compare the size of the associations of the exposure and the instrument with the covariates. […] We calculate confidence intervals around both bias terms to indicate uncertainty.”

Author details

1. Neil Martin Davies

   1. Medical Research Council Integrative Epidemiology Unit, University of Bristol, Bristol, United Kingdom
   2. Bristol Medical School, University of Bristol, Bristol, United Kingdom

   Contribution

   Conceptualization, Data curation, Formal analysis, Funding acquisition, Visualization, Writing—original draft, Project administration, Writing—review and editing

   For correspondence

   neil.davies@bristol.ac.uk

   Competing interests

   reports a grant for research unrelated to this work from the Global Research Awards for Nicotine Dependence (GRAND), an independent grant making body funded by Pfizer.

   "This ORCID iD identifies the author of this article:" 0000-0002-2460-0508

2. W David Hill

   1. Centre for Cognitive Ageing and Cognitive Epidemiology, University of Edinburgh, Edinburgh, United Kingdom
   2. Department of Psychology, University of Edinburgh, Edinburgh, United Kingdom

   Contribution

   Data curation, Writing—review and editing

   Competing interests

   No competing interests declared

3. Emma L Anderson

   1. Medical Research Council Integrative Epidemiology Unit, University of Bristol, Bristol, United Kingdom
   2. Bristol Medical School, University of Bristol, Bristol, United Kingdom

   Contribution

   Methodology, Writing—review and editing

   Competing interests

   No competing interests declared

4. Eleanor Sanderson

   1. Medical Research Council Integrative Epidemiology Unit, University of Bristol, Bristol, United Kingdom
   2. Bristol Medical School, University of Bristol, Bristol, United Kingdom

   Contribution

   Methodology, Writing—review and editing

   Competing interests

   No competing interests declared

5. Ian J Deary

   1. Centre for Cognitive Ageing and Cognitive Epidemiology, University of Edinburgh, Edinburgh, United Kingdom
   2. Department of Psychology, University of Edinburgh, Edinburgh, United Kingdom

   Contribution

   Data curation, Funding acquisition, Writing—review and editing

   Competing interests

   No competing interests declared

6. George Davey Smith

   1. Medical Research Council Integrative Epidemiology Unit, University of Bristol, Bristol, United Kingdom
   2. Bristol Medical School, University of Bristol, Bristol, United Kingdom

   Contribution

   Conceptualization, Funding acquisition, Methodology, Writing—review and editing

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0002-1407-8314

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