Education and coronary heart disease: mendelian randomisation studyBMJ 2017; 358 doi: https://doi.org/10.1136/bmj.j3542 (Published 30 August 2017) Cite this as: BMJ 2017;358:j3542
All rapid responses
We are grateful to Doidge and Dearden for their comprehensive articulation of why our paper might appear invalid. We will respond to the three critiques in order of their proposal, of which the first might be the most important.
Please see the figure here:
This figure illustrates three competing interpretations of our data and the wider literature. Panel A shows our interpretation, whereby low education causes heart disease. Panels B and C illustrate two alternative interpretations where low education does not cause heart disease. Our study used 162 single-nucleotide polymorphisms (SNPs) to provide evidence of a causal relationship between education and coronary heart disease. We use unbroken arrows to denote causal pathways that we believe to exist, and we use dashed arrows to denote hypothetical causal pathways that critics may posit to exist alternatively.
Looking at panel A, the dark grey arrow represents one particular SNP (hereinafter “the first SNP”), while the lighter grey arrows denote associations from other SNPs (e.g. “the second, third, fourth, SNPs”, etc.). Due to limited space, we have not drawn all 162 arrows and ask readers to imagine the remaining arrows. In the same way, arrows marked with the darkest blue or green represent effects arising from one particular SNP (such as “the first SNP”) while arrows marked with a lighter colour denote effects arising from another SNP (such as “the second SNP”).
In panel B, the first SNP has two causal effects – the dark grey arrow denotes the first effect on brain function, while the dark blue dotted arrow denotes a putative effect of the same SNP on cardiovascular function. In panel C, the first SNP also has two causal effects, whereby both of these arise as a consequence of altered brain function – the first dotted dark green arrow (labelled A) denotes a putative effect on education, while the second dark arrow (labelled B) denotes a putative effect on heart disease. The core finding which we are seeking to explain with these various models is: how is it that across a large set of 162 SNPs, the magnitude of association with education is linearly correlated with the magnitude of association with heart disease?
The blue arrows in panel B illustrate the conventional understanding of pleiotropy (as detailed in Supplementary Figure 1 of our main paper). The results of our sensitivity analyses (and the wider literature) make these blue arrows unlikely. This we discussed at length in our main paper, and it appears to be an unlikely source of recent criticisms. Briefly, it would be implausible for the SNP with the strongest association with education (e.g. the first SNP, illustrated with the dark grey arrow) to also, by coincidence, have the strongest association with heart disease (e.g. illustrated with the dashed dark blue arrow). A similar correlation would have to occur, by coincidence, between the strength of association from SNP-to-education, and the strength of association from SNP-to-heart disease, for the remaining 161 SNPs (illustrated with lighter grey and blue colours).
One potential cause of differences of opinion might lie in whether our sensitivity analyses are useful for inferring the likelihood of panel C occurring. Here, the common pleiotropic pathways, which cause changes to education and heart disease, are restricted to originate from a common alteration to brain function. That is, while in the middle panel, a pleiotropic SNP may cause changes to cardiovascular tissues directly, in the bottom panel such changes have to be first mediated via a common neurological cause. We maintain that our sensitivity analyses are also informative here, and our results imply that the green dashed arrows in panel C are unlikely to account for our findings. The crux of our argument is the same as in panel B: that those SNPs which are most strongly associated with education (i.e. dark green arrow A) also show the strongest association with heart disease (dark green arrow B). In other words, it would require that the causal effect measured by one SNP is comparatively homogeneous to the causal effects measured by another SNP (further evidence of this is provided in our supplementary methods 220.127.116.11).
When evaluating the plausibility of panel C, a central question to ask is whether the unknown intermediating phenotype(s) posited by critics, which sit in the green box that lies between SNPs and heart disease, is composed of a single phenotype with a large effect on heart disease, or alternatively it is composed of multiple phenotypes where each one contributes a small effect on heart disease. First, let’s consider the simpler scenario that only one intermediating phenotype exists inside this green box. If this is true, it may well invalidate our InSIDE assumption (INstrument Strength Independent of Direct Effect), since those instrumented SNPs with the largest association with education are also associated more strongly with a direct effect on heart disease. A violation of the InSIDE assumption is practically required, in order to invalidate the MR-Egger findings that otherwise support the causal interpretation from Panel A. However, we find the biological plausibility of this scenario to be less likely. It appears more plausible that the top 162 genetic hits for education would denote more than one causal mechanism from genetic variants to education. Second, let’s consider the alternative scenario, which we find biologically more plausible - that there are multiple intermediating phenotypes inside the green box, to account for multiple mechanisms from genetic variants to education. This scenario however, makes it less likely for the InSIDE assumption to be violated. Such violation would require that when looking across these multiple phenotypes, altogether they present a linear pattern of dose-response confounding, whereby the strength of A would have to correlate with the strength of B. Such correlation may happen, by chance, if there are only two or three phenotypes. However, this correlation becomes increasingly unlikely as one approaches a longer list of intermediary phenotypes. In other words, we assume that at least some of our 162 instruments are “mechanistically separate instruments” (which we could define as “instruments whose mechanism of action on education varies between one instrument and another”). By assuming different mechanisms, we are better placed to empirically probe the question of whether parallel pleiotropic causal arrows (such as the dashed green “B” arrows) could extend from the instrument to the outcome.
We concede that the arguments presented so far may not be sufficient, on their own, to provide complete reassurance that our assumptions have not been violated. This conclusion can only be made after considering additional sources of inference (such as the plausibility of specific candidate confounders, as well as consistency with causal inferences from entirely different methods).
Let’s consider the empirical evidence from the wider literature for and against specific candidate confounders that could potentially lie in the green box. This we discussed in detail during peer review (available on http://www.bmj.com/sites/default/files/attachments/bmj-article/pre-pub-h... pp. 18-20) with reference to two examples (intelligence and personality). As for intelligence, the body of evidence appears to suggest that intelligence can be a causal mediator along the pathway from education to heart disease. This is most compatible with panel A, which is what we think reflects the most likely causal pathway. Alternatively, critics could posit that genetic predisposition to greater intelligence may theoretically be a pleiotropic confounder (located in the green box of panel C), which invalidates our MR and observational analyses. However, this model is difficult to reconcile with the causal effects measured by natural experiments and twin studies. In both of those cases, causal effects are elicited by varying the environmental (i.e. non-genetic) component of education. Although it is possible for other biases in these study designs to coincidentally align with this bias in our MR and observational results, the probability of this appears to be low to us. The second example we discussed in peer review was personality (also called temperament). Theoretically, this could arise from altered brain function to influence both education and heart disease. However, the empirical evidence suggests that those personality traits which associate with education (i.e. conscientiousness) are not associated with heart disease. And those personality traits which associate with heart disease (i.e. neuroticism) are not associated with education (whereby both conscientiousness and neuroticism do not covary). We would welcome suggestions about a specific personality trait that might associate with both education as well as with heart disease, as theoretically this remains possible.
The second criticism that Doidge and Dearden mention is that ethnicity might be a confounder that associates with both our instruments (SNPs) and heart disease. We think this is unlikely, since the GWAS data we analysed have been carefully selected to only include individuals of one broad ethnic group – people of European origin. By excluding people of non-European ancestry, this removed the larger ethnic confounders that one might see in Western countries. Furthermore, the GWAS data we used additionally controlled for the top principal components of the genetic-relatedness matrix, which should further reduce residual confounding by ethnicity differences within Europeans.
The third criticism that Doidge and Dearden mention is how our causal point estimate is larger than our observational point estimate. However, the confidence intervals of these two measures overlap, and so this difference may have simply arisen due to chance alone. In the absence of any statistical evidence, we think it’s more appropriate to conclude that our causal and observational estimates are similar to each other. Furthermore, it is possible that observational measures of education are prone to larger measurement error, while genetic allocation into educational groups may be prone to less measurement error. This may suggest that the observational estimate could be slightly biased towards the null, while our Mendelian randomization estimate may be closer to the true causal effect.
Finally, we wish to reiterate the importance of triangulating the results of Mendelian randomisation studies alongside causal inferences from completely different methods (e.g. policy experiments, and twin studies), as we elaborate in the discussion of our paper. Alignment of results from multiple sources employing orthogonal approaches further increases the probability that our assumptions are not violated.  This also raises the threshold of evidence required from critics who hold the opposing view, before they can persuade readers of the validity of their model. In our view, the evidence is substantially larger for, than against, causal effects arising from more education to reductions in heart disease in the settings of the studies we have utilised. For social processes, such as the effects of education, it is perfectly reasonable to anticipate that the effects of more education could vary between different contexts and time periods; this does not detract from them being causes, however.
As for the question of when Mendelian randomisation analyses go beyond their limits, then we agree that we have pushed the boundaries of what is feasible in this arena, perhaps in two ways. First, by comprehensively examining a socioeconomic exposure which is relatively upstream in disease aetiology, and second, by using instruments whose biology is less understood than in some previous Mendelian randomisation analyses. While we agree that this increases uncertainty, in our view, careful exploration is nonetheless increasingly warranted in situations where: 1) observational effects are large but randomised trials are infeasible; 2) many “mechanistically separate instruments” exist, with which to power sensitivity analyses; and 3) orthogonal sources of causal inference exist, with which findings can be triangulated. We hope that judicious application of Mendelian randomisation, and comprehensive consideration of sensitivity analyses as well as the wider literature, can help foster greater understanding of the role of social factors in the genesis of disease.
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3 Jokela M, Pulkki-Råback L, Elovainio M, Kivimäki M. Personality traits as risk factors for stroke and coronary heart disease mortality: pooled analysis of three cohort studies. Journal of behavioral medicine. 2014 Oct 1;37(5):881-9.
4 Okbay A, Beauchamp JP, Fontana MA, Lee JJ, Pers TH, Rietveld CA, Turley P, Chen GB, Emilsson V, Meddens SF, Oskarsson S. Genomewide association study identifies 74 loci associated with educational attainment. Nature. 2016; 533(7604):539-42.
5 Lawlor DA, et al. Triangulation and aetiological epidemiology. Int J Epidemiol. 2016;45:1866-1886.
Competing interests: No competing interests
We are grateful to the four rapid responses. In this response, we reply to the first three rapid responses (by Saripanidis, Bhanwra and Anand).
Saripanidis highlights the important problem of low scientific literacy in large segments of the general public. Saripanidis suggests that this may be one obstacle towards implementing educational reforms. While this does create additional challenges, we think that the research and policy community can respond by effectively communicating these findings simply and persuasively (for example, by using video abstracts like we did). Saripanidis’ dissatisfaction with low scientific literacy highlights to us, another reason why societies need to invest more in education. Others before us have noted other societal benefits to raising education, and we would like to add to this that health too could benefit. Second, Saripanidis suggests that the low cost-effectiveness of educational interventions is one reason for being pessimistic about their feasibility. We are more optimistic. First, there is a large body of evidence to suggest that investments in education generate substantial returns to the individual and to society at large in economic terms. At the individual level, they seem to increase the salary of those individuals who have been educated; and at the population level they may increase Gross Domestic Product. Second, even if these wider economic benefits are ignored, and one takes purely a health-economic orientation, it is plausible that educational interventions might be cost effective. For example, let’s assume that 33% of people develop coronary heart disease (CHD) in their lifetime, that 3.6 years of education prevents one third of CHD, that each CHD event prevented creates 10 QALYs in that person, and that cost-effective interventions should cost less than £20 000 per QALY. Under this scenario and with a very simplistic model, an intervention which costs less than £6’000 to create one additional year of education may appear to be cost-effective. Although we have no data on what such an intervention would look like, we note how mainstream political parties in the UK have recently suggested educational policies that cost more than this. This suggests that investing public money to increase education might be both cost-effective and politically feasible. Nonetheless, formal cost-effectiveness analysis would be needed to answer this question more accurately, particularly to select an appropriate discounting rate in light of the long lag between intervention and disease.
We are grateful to Sangeeta Bhanwra for her warm words of support for our article, and for urging governments and health policy makers to consider attending to policies that increase educational attainment. We would like to add that if possible, this could be accompanied by monitoring, where the real-life impact of such reforms on health behaviours and cardiovascular risk factors is evaluated as rigorously as possible.
Anand makes three points.
1) “European ancestry” might be too large a group. Indeed, residual confounding by ethnicity is one potential weakness to consider. We recognize that some smaller ethnic differences may remain in these GWAS samples (for examples, including Hispanic and Scandinavian persons), however such subgroups are quite rare in number, and their inter-group differences also quite small, for them to drive the large effects that we see. For example, participants from Finland, Sweden and Norway formed just 7% of the analytical sample of the education GWAS, while participants from the UK and USA formed 58% of the analytical sample. Furthermore, the GWAS data we used additionally controlled for the top principal components of the genetic-relatedness matrix, which should further reduce residual confounding by ethnicity differences within Europeans.
2) We defined “Educational attainment” by asking participants to report the highest qualification that they have. This was used to create a categorical variable, with multiple choices. To facilitate greater statistical power, this categorical variable was then transformed into a continuous variable. This was done by mapping each increase in educational category to the average number of years that participants usually have to study, in order to obtain that qualification. Such mapping was personalized to each country context, as per ISCED criteria.
3) Our study was conducted in High Income countries, as defined by the World Bank criteria. We agree that persons on a low income, who live in a High-Income country, will have a shorter and potentially less enjoyable life, when compared to comparable persons on a higher income in the same country. However, we think that this is not a methodological problem in our study – instead this is the real-world problem which our study seeks to inform. For example, if policies that increase educational attainment are implemented with the guiding principle of Proportionate Universalism, then this might be one way to lower inequalities of income within countries, and thereby also lowering inequalities in health and well-being within countries.
 Homer-Dixon T. The Ingenuity Gap. Knopf: 2000
 McIntyre N. Labour will scrap tuition fees and address growing student debt, vows John McDonnell. The Independent. 25 Sept 2017 Available from: http://www.independent.co.uk/news/uk/politics/labour-tuition-fees-scrap-...
Competing interests: No competing interests
Tillmann, et al. ’s analysis of the effects of education on coronary heart disease (CHD) makes some strong claims about the causality of their estimated effects. These claims are based on the presumption that Mendelian randomisation removed confounding in the relationship between education and CHD. There are at least two good reasons to be sceptical of this assumption and we strongly contend that these should not be viewed as causal effect estimates. First we’ll examine the author’s assumptions about confounding, then we’ll examine the results that they present.
Mendelian randomisation is an application of instrumental variable analysis, which economists have long used to study causal effects where the potential for interventional research is limited, such as education . As with any other instrumental variable analysis, the validity of Mendelian randomisation depends critically on the absence of a relationship between the instrument (genes) and the outcome (coronary heart disease), other than that which operates through the exposure (education). Richards and Evans  break this assumption down further into an absence of direct effects (“assumption 2”) and an absence of association with confounders (“assumption 3”).
In most Mendelian randomisation studies, the prime suspect for violation of assumption 2 is genetic pleiotropy—multiple actions of single genes. Tillmann, et al.  go to great lengths to test for genetic pleiotropy but this is misdirected, as we shall explain. Richards and Evans  propose that assumption 3—association with confounders—is unlikely to be violated by “all or even most of the 162 genetic determinants of educational attainment” (p.2). We counter that it is highly likely that every single ‘genetic determinant of educational attainment’ breaks one or other of these assumptions. The reason for this is simply that there is no plausible explanation presented by the authors or conceivable to us which doesn’t. Every possible way that a gene could be associated with educational attainment involves either mediators that are themselves potential confounders of the relationship between education and CHD, or confounders of the gene–education relationship that may also confound the education–CHD relationship. Richards and Evans  dismissal of potential confounding by cognitive ability ignores the fact that something must fill the gap between genes and education, because genes cannot possibly affect education directly.
The most plausible mechanism for explaining a relationship between genes and education is an effect of the genes on brain function, whether it be academic intelligence, mental health, behaviour or temperament (Figure 1). Each of these is likely to influence educational attainment and could conceivably also influence CHD. What’s important to note is that these do not represent genetic pleiotropy; they require only a single effect of a gene on a physiological mediator, and it is the physiological mediators that in turn affect both educational attainment and CHD. The authors do discuss the literature on twin studies, which may reduce this type of confounding, but Mendelian randomisation cannot.
The other plausible explanations for associations between genes and education is what Tillmann, et al.  acknowledge as ‘dynastic effects’, such as “when parental genes associate with parental behaviours that directly cause [both education and] a health outcome in the child”. Mendelian randomisation studies often rely on huge samples to overcome the limitations of genetic instruments that are only weakly correlated with the exposures of interest. When the exposure and outcome variables are both correlated with ethnicity (as education and CHD are), then dynastic effects may be a significant limitation. In the absence of ethnic or cultural control, genetic instruments may simply be detecting cultural confounding. The authors’ argument about the weak relationship between parents’ and offspring’s education is not directly relevant because it is the relationship between parents’ genes and offspring’s education that is of most concern.
Figure 1 Alternative causal diagram to explain associations between genes, education and coronary heart disease (CHD). Note: there can be no direct effect of genes on education. https://ibb.co/fNtxJa
Now let’s examine the estimates presented. Given the depressingly modest effect sizes seen in most dietary and lifestyle interventions that target reductions in CHD specifically, the large effect size produced by this analysis should have raised a red flag. An even bigger red flag is raised by examining the relative effect sizes estimated by the authors in their ‘observational’ and ‘causal’ analyses; the Mendelian randomisation estimates are stronger than the minimally adjusted regression estimates. If the Mendelian randomisation estimates are truly causal effects, then the unobserved confounders in the regression estimates (e.g. socioeconomic status) must be inversely correlated with education and health. This is generally not the case; confounders like socioeconomic status affect education and health in the same direction and bias regression estimates away from the null. Thus, the authors’ own results provide evidence to indicate that this is an example of an invalid instrument yielding biased results.
Mendelian randomisation is an extremely valuable analysis tool, but this application has stretched it beyond its useful limits. The gap in the causal chain between genes and educational is too great. Mendelian randomisation should be used to explore modifiable factors closely related to physiological phenotypes and environmental factors far removed should be left for other designs. Strong claims of causality cannot be justified when the assumptions required for instrumental variable analysis are so easily violated. For further discussion of the sensitivity of education effects to instrumental variable selection, see Blundell, et al.  and for a more general guidance on instrumental variable analysis and its limitations, to Angrist and Pischke .
James Doidge*, Administrative Data Research Centre for England, University College London; Centre for Population Health Research, University of South Australia
Lorraine Dearden, Institute for Fiscal Studies; UCL Institute of Education, University College London
*Correspondence to J.Doidge@ucl.ac.uk, 222 Euston Road, London NW1 2DA, UK
1. Tillmann T, Vaucher J, Okbay A, et al. Education and coronary heart disease: Mendelian randomisation study. BMJ 2017;358 doi: 10.1136/bmj.j3542
2. Blundell R, Dearden L, Sianesi B. Evaluating the effect of education on earnings: Models, methods and results from the National Child Development Survey. Journal of the Royal Statistical Society: Series A (Statistics in Society) 2005;168(3):473-512. doi: 10.1111/j.1467-985X.2004.00360.x
3. Richards JB, Evans DM. Back to school to protect against coronary heart disease? BMJ 2017;358 doi: 10.1136/bmj.j3849
4. Angrist JD, Pischke J-S. Instrumental variables in action: Sometimes you get what you need. Mostly harmless econometrics: An empiricist's companion: Princeton University Press 2009.
Competing interests: No competing interests
1. European populations. Pray what is the definition of European? Are the reindeer herders of Scandinavia European for the purposes of this research ?
2. Education. The authors seem to mix up YEARS OF EDUCATION and EDUCATIONAL ATTAINMENT.
What exactly is education?
3. They talk of High Income countries. Is life in a country with HIGH GDP necessarily equally good for rich persons and poor persons?
I appreciate that Mendelian randomisation is being applied. But it would be reasonable to expect a little more careful use of terminology.
Competing interests: No competing interests
Education : A Meaningful Addition to Non-Pharmacological Measures for protection against Coronary Artery Disease
It is a wonderful effort by the authors to determine the relation between education and risk of coronary artery disease (CAD) and highlight the lack of education as a causal risk factor. As the randomised trials in this field are not practical, by using the Mendelian Randomisation Study the authors have very well presented the hypothesis, that low education is a causal risk factor in the development of coronary heart disease.
Risk factors like smoking, high body mass index, increased triglycerides were found to be reduced with education, and higher high density lipoprotein cholesterol (the protective cholesterol) was increased in this study. The longer period of education has a significant effect on decreasing the risk by affecting the risk factors.
The Government and policy makers have always been implementing campaigns & methods to create awareness amongst the public to reduce smoking, promoting physical activity and other non-pharmacological measures to reduce risk of disease like CAD. The efforts need to be increased on the same lines to emphasise the role and importance of education also in reducing these risk factors.
Competing interests: No competing interests
Low education with diminished scientific and health literacy afflicts large percentages of UK and US adult population.
Such patients, in these Countries, are at increased risk for coronary heart disease.
Increasing education in order to achieve future health benefits seems way too optimistic and expensive.
Millions of people persistently resist any new scientific notion.
Competing interests: No competing interests