Department of Preventive Medicine, University of Southern California, Los Angeles, CA 9089-9011, USA
This issue of the International Journal of Epidemiology reprints a seminal letter to the editor by Martijn Katan,1 which appears to be the first description of the concept of Mendelian randomization. In discussing the controversy over whether the association between low serum cholesterol and cancer is causal or might simply reflect an effect of the disease to lower cholesterol levels (reverse causation) or confounding by diet or other factors, Katan proposed a test of causality by studying instead the relationship between cancer and a genetic determinant of serum cholesterol, the apolipoprotein A (APOE) gene. His rationale was that since alleles are allocated essentially at random, such an association would not be subject to either confounding or reverse causation. Thus, if a causal relationship between APOE and serum cholesterol were clearly established, then an association between APOE and cancer would provide indirect evidence for the causality of the association between serum cholesterol and cancer. Although Katan did not use the term Mendelian randomization, the concept has been attributed to him and subsequently developed by a number of other authors.26 In particular, Davey Smith and Ebrahim2 have shown how the magnitude of the estimated effects of a gene (G) on an intermediate phenotype (IP) and on disease (D) can be combined to yield an estimate of the causal effect of the intermediate phenotype on disease, as illustrated in the following figure:
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Use of instrumental variables in epidemiology |
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Complications |
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This would be a case of a false-positive inferencean incorrect conclusion that there is a causal connection between IP and D when in fact none exists. Of course, negative confounding could also lead to a false-negative conclusionthat there was no association between IP and D when there really is one.
One way such a situation could come about is when a single gene has pleiotropic effects. Suppose, for argument sake, that the true causal picture were as follows:
For example, Davey Smith and Ebrahim2 provide an interesting discussion of the role of folate, homocysteine, and the methylenetetrahydrofolate reductase (MTHFR) gene in the aetiology of coronary heart disease (CHD) and neural tube defects (NTD). This is a very complex pathway, involving several feedback loops. For CHD, we agree with their assessment that the similarity of the direct estimate of the association between homocysteine and CHD and the indirect estimate based on the associations of each with MTHFR supports a causal interpretation. For NTD, on the other hand, they find a similar concordance of the estimates, but a causal interpretation seems less appropriate. We think it more likely that the second picture applies here, where IP1 might represent homocysteine and IP2 folate availability.6,15,16 Nevertheless, whether homocysteine or serum folate is the proximal cause of NTD, an intervention to increase dietary folate could be an effective preventive measure.
Although G may be the ultimate determinant of IP, many other factors can induce expression of G, so that associations between IP and D could better reflect that proximal causal relationship than the more distant GD association. Davey Smith and Ibrahim discuss the complications posed by the phenomenon of canalization, the buffering of effects of genetic or environmental influences to maintain homeostatic equilibrium, via such mechanisms as alternative metabolic pathways, possibly regulated by different genes. On the other hand, G remains constant over time and is generally measured with a high degree of accuracy, whereas IP varies throughout the aetiologically relevant period and a measurement at a single point in time may subject to a large amount of measurement error (or even bias in the case of reverse causation). These are well-known advantages of the instrumental variables approach, which apply equally to Mendelian randomization.
Geneenvironment interactions
The diagrams we have considered so far do not include any external environmental factors or geneenvironment (G x E) interactions. Such a model might be represented schematically as follows:
Even in linear models, it seems a stretch to conclude that:
the association of genotype with NTD risk ...demonstrates that an environmental intervention may benefit the whole population, independently of the genotype of individuals receiving the intervention2
at least without good observational evidence about the association of exposure and disease within genotype. One would also want to see evidence that changes in exposure actually lead to changes in disease risk, particularly in complex systems where there are multiple points at which different genetic and environmental perturbations may lead to various phenotypic outcomes.6
Clayton and McKeigue3 have argued that:
Despite current enthusiasm for study of geneenvironment interactions, the closely related issue of how to define and interpret interaction between environmental factors remains unresolved after two decades of debate. ... We suggest that epidemiologists should focus instead on use of genetic associations to test hypotheses about causal pathways amenable to intervention. ... In this example [NAT and heterocyclic amines in cooked meat], as with the MTHFR gene, there is a possible biological interaction between genotype and dietary intake, but testing for statistical interactions between genotype and dietary intake would not contribute much to our understanding of these biological interactions or to our ability to exploit them in disease prevention. ... The prospects for epidemiology in the post-genome era depend on understanding how to use genetic associations to test hypotheses about causal pathways, rather than on modeling the joint effects of genotype and environment.
Part of their argument relies on the observation that power to test main effects will often be much better than for interactions, although there are exceptions.17 Hence the opportunity to exploit Mendelian randomization to assess causality is a great advantage of tests of pure genetic main effects. Indeed, the track record of replication of reports of G x E interactions seems to be even more dismal than for main effects of gene associations,1820 perhaps in large part because such studies are frequently underpowered, involve some data dredging, and are subject to publication bias. We generally agree with their conclusion that:
A case-control study of the relation between the TT genotype [of MTHFR] and risk of neural tube defect can be interpreted as equivalent to a randomized trial of the effect on disease risk of alteration of the availability of folate3 [emphasis added].
Genegene interactions
The same picture might apply if one were to replace E by another gene, say H. It is quite conceivable that a second causal variant may exist within the same candidate gene region and be in linkage disequilibrium with G. The lack of independence between H and G may lead to substantial bias in the estimation of the GD association.6 Furthermore, by the same line of argument as above for non-linear models, if IP were determined by two genes (either independently or in some interactive manner), but one only assessed G, then the association between IP and D estimated from the associations of each with G would also be biased. In particular, a false-negative conclusion could be reached if H were really the more relevant determinant of IP and failure to account for it led to a null result for the GD association. As with G x E, failure to account for G x G interactions could also lead to either false-positive or false-negative inferences.
Population stratification
A reservation about the broad conclusion Mendelian randomization is equivalent to a randomized trial is that GD associations from case-control studies are susceptible to distortion by population stratification.6 Not only substantial genetic differences in populations, but more subtle clustering of genetically similar individuals within the population, can bias a test of the GD association.21 Although some have argued that population stratification may not be a serious concern, at least in Caucasian populations of European descent,22,23 this problem can be overcome by appropriate design or analysis. The low power of Mendelian randomization compared with direct tests of association implies that very large sample sizes will be required. Unfortunately, the problem of inflation of Type I Error rates by population stratification will only increase with increasing sample size, as smaller and smaller biases will become significant.
To fully exploit the power of Mendelian randomization, one should consider using the case-parent-triad design that is based on the random transmission of alleles from parents to offspring and is therefore robust to population stratification.24,25 Similar properties are shared by other family-based association tests (FBAT), such as a sib case-control design and those that exploit both parents and siblings or even extended pedigrees.2629
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Conclusions |
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Biological pathways are extremely complex, so a simple triangulation picture will almost certainly be wrong in most situations. However, our understanding of these pathways will doubtless continue to improve (and hence the pictures will get more and more complicated), but on the other hand, prospects for overcoming confounding and reverse causation in traditional observational studies of the IPD association are very limited. In the long run, the concept of Mendelian randomization may prove to be a valuable way for epidemiology to move beyond its limits. Thus, the conditions for its validity deserve careful consideration.
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Appendix |
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Then,
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The derivation above assumes that the model is correctly specified. In the main body of our article, we describe several ways the model could be misspecified and the implications for bias. For example, suppose G has a direct effect on D, independent of IP, say E(D|IP) = ß0 + ß1IP + ß2G. Then it is easy to see that 1/
1 estimates ß1 + ß2/
1, and thus will yield a biased estimate of the causal effect of IP on D. Alternatively, suppose there is another factor that influences IP, say H, which could be another gene or some environmental factor. Suppose first that H has no direct effect on D other than through its influence on IP, and G and H are independent and contribute additively to IP, that is, E(IP|G,H) =
0 +
1G +
2H. Then even if H is ignored,
1/
1 still estimates ß1, although its variance will be increased. However, if G and H are associated in the population or if they have an interactive effect on IP, then both
1 and
1 will be biased, but to the same extent, so their ratio
1/
1 turns out to be a consistent estimator of ß1 (assuming there is no direct effect of G or H on D except through IP). To see this, suppose E(H|G) =
0 +
1G. Then if E(IP|G,H) =
0 +
1G +
2H, then E(IP|G) =
0 +
1G +
2E(H|G) =
0* +
1* G, where
0* =
0 +
2
0 and
1* =
1 +
2
1. Likewise, if E(D|IP,G,H) = ß0 + ß1IP, then E(D|G) = ß0 + ß1E[IP|G,E(H|G)] =
0* +
1*G, where
0* = ß0 + ß1(
0 +
2
0) and
1* = ß1(
1 +
2
1). Thus
1*/
1* = ß1(
1 +
2
1)/(
1 +
2
1) = ß1. This also applies if G and H have an interactive effect on IP (but no direct effects on D), provided the estimates of the GD and GIP associations derive from the same dataset or studies with the same joint distribution of G and H.
For dichotomous disease traits, the derivation is somewhat more complex and the conditions for validity are more restrictive. The most tractable situation is when IP N(
0 +
1G,
2) and ln[Pr(D = 1|IP)] = ß0 + ß1IP for a rare disease. Then it is easily shown that ln[Pr(D = 1|G)] =
0 +
1G, where
0 = ß0 + ß1
0 + ß12
2/2 and
1 =
1ß1, so
1/
1 is a consistent estimator of ß1, just as in the linear model. For a probit link, the corresponding expression is ß1 =
1/
(
12 −
12
2), without the need for a rare disease assumption, but now the ratio
1/
1 is only an approximate estimator of ß1. Closed-form solutions are not available for the logistic model, but qualitatively the behaviour is similar.14 As before, a direct effect of G on D will yield a biased estimator.
Unlike the linear model, however, if there is another factor H influencing IP, then if G and H are not independent, the estimators 1 and
1 are both biased, but these biases may no longer cancel out exactly. Suppose that ln[Pr(D = 1|IP)] = ß0 + ß1IP and IP
N(
0 +
1G +
2H,
2). If H
N(
0 +
1G,
2) and H is ignored, then IP
N(
0* +
1*G,
2 +
22
2), where
1* =
1 +
2
1, and ln[Pr(D = 1|G)] =
0* +
1*G, where
1* = ß1(
1 +
2
1), so in this case
1/
1 is indeed a consistent estimator of ß1. But now suppose instead that H were dichotomous, with Pr(H = 1|G) = pG. Then
1* = ß1
1 + ln[1 + p1 exp(ß1
2)] − ln[1 + p0 exp(ß1
2)] and
1* =
1 +
2(p1 − p0). Thus
1*/
1* will not estimate ß1 unless p1 = p0 or
2 = 0 or ß2 = 0.
In general, the validity of Mendelian randomization lies in the equivalency of 1ß1 =
1. That is, the association between GIP and IPD is assumed to be equivalent to the GD relation. If g(D|·) gives the functional relation between an exposure and the disease outcome and h(IP|G) gives the relation between the gene variant and the intermediate phenotype, then for Mendelian randomization estimates to be valid, it must be possible to write g(D|G,
1) =
g(D|IP,ß1) h(IP|G,
1) d IP as g(D|G,
1ß1). This holds if h(·) is conjugate to g(·).
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References |
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