Mendelian randomization (MR) uses genetic variants as a natural experiment in observational studies to investigate potential causal effects of modifiable risk factors on health outcomes (Davey Smith and Ebrahim, 2003). MR is often conducted in two homogeneous study populations, i.e., two-sample MR (Burgess et al., 2015). MR is thought to be robust to the confounding that often occurs in conventional observational studies due to the random allocation of genetic endowment at conception being used as a proxy for the exposure (Burgess et al., 2012; Davies et al., 2018). Currently, MR is a popular approach for assessing causality (Sekula et al., 2016). However, MR estimate rests on stringent assumptions, as illustrated using directed acyclic graphs (DAGs) in Figures 1A,B (Davey Smith and Ebrahim, 2003; Lawlor et al., 2008).

• IV1 (the relevance assumption): the genetic variant is robustly associated with the exposure of interest;

Notably, aside from IV1 that can be empirically verified using the F-statistic (Staiger and Stock, 1997; Bowden et al., 2016a), IV2 and IV3 are typically harder to justify. Hence, violations of these assumptions can occur, leading to misleading conclusions. Of these, selection bias is increasingly acknowledged as distorting MR estimates in the selected populations investigated (Nitsch et al., 2006; VanderWeele et al., 2014; Canan et al., 2017; Vansteelandt et al., 2018a; Vansteelandt et al., 2018b; Munafò et al., 2018; Munafò and Smith, 2018; Gkatzionis and Burgess, 2019; Smit et al., 2019; Schooling et al., 2020) and has largely focused on bias arising from selection on exposure (Vansteelandt et al., 2018a; Vansteelandt et al., 2018b; Munafò et al., 2018; Gkatzionis and Burgess, 2019; Smit et al., 2019).

Genetic studies are usually carefully designed to avoid selecting sample on genetic make-up and phenotypes. Generally, selection bias occurs in an MR study when the sample in the original genome-wide association study (GWAS) are selected conditional on survival until study recruitment on genotype of interest in the presence of prior death from the outcome or competing risks of the outcome (Figure 1C), especially in the original outcome GWAS (Schooling et al., 2020). The problem is the time lag between genetic randomization at conception and recruitment of participants into the GWAS. Participants diagnosed with or dead from the outcome or a competing risk of the outcome are not recruited into the outcome GWAS, which attenuates or reverses MR estimates for harmful exposures, because people who have already died of their harmful genetic endowment and people who have died of the outcome or a competing risk of the outcome are missing. As such, selection bias may create a spurious genetic variant–outcome association by opening the backdoor path from genetic instruments to the outcome of interest, violating the IV3 assumption.

For example, previous observational studies showed that higher transferrin binds to circulating iron and influences iron status, which may further cause iron-deficiency anemia and increase the risk of stroke (Chang et al., 2013; Marniemi et al., 2005; Gillum et al., 1996). However, a recent MR study reported that lower iron status also appeared to protect against stroke (van der et al., 2005; Gill et al., 2018), especially cardioembolic stroke (Gill et al., 2018). An increasingly acknowledged explanation is selection bias, possibly due to the presence of competing risks [e.g., coronary artery disease (Gill et al., 2017), hypercholesterolemia (Gill et al., 2019), chronic kidney disease (Fishbane et al., 2009), skin infections (Gill et al., 2019), liver disorders (e.g., hepatitis C) (Shan et al., 2005), and rheumatoid arthritis (Yuan and Larsson, 2020)] caused by the shared confounders (e.g., socioeconomic position, lifestyle, and health status), affecting survival of the underlying population (Camaschella, 2015; McLean et al., 2009), as shown in Figure 2. For instance, people with competing risks, such as coronary artery disease, tend to die earlier than those with stroke in Western settings (Kesteloot and Decramer, 2008; Menotti et al., 2019; Diseases and Injuries, 2020). As such, people vulnerable to these competing risks with higher iron status may die before study recruitment, leaving more “healthier” participants in the study and inducing biased estimates.

Several statistical methods have been proposed to detect and eliminate selection bias in MR studies, most of which focus on bias arising from selection on exposure (Bareinboim and Pearl, 2012; Arnold and Ercumen, 2016; Hemani et al., 2017; Tchetgen Tchetgen and Wirth, 2017; Vansteelandt et al., 2018a; Brumpton et al., 2020; Zhao et al., 2020; Sanderson et al., 2021; Wang and Han, 2021), which is generally thought to have limited effects. However, selection on genetic endowment and outcome or competing risk of the outcome is more pervasive (Schooling et al., 2020) and can have larger effects. One approach that has not been considered is the use of a “negative control,” which has been widely used in laboratory science for decades to help detect problems with the experimental method (Arnold and Ercumen, 2016). In epidemiological studies, a formal approach has been described in detail and suggested as a means of detecting residual confounding, selection bias, and measurement bias (Lipsitch et al., 2010; Arnold et al., 2016). Recently, negative control outcomes, defined as sharing identical confounders with the exposure–outcome association but not associated with the exposure, have been proposed to detect potential population stratification in MR studies (Sanderson et al., 2021). Other approaches include summary data-based MR [SMR, e.g., MR robust adjusted profile score (MR-RAPS)] (Zhao et al., 2020; Wang and Han, 2021), two-sample MR Steiger method (Hemani et al., 2017), and three-sample MR (Zhao et al., 2019), in which the selection procedure of genetic instrument (e.g., winner’s curse) is considered a form of selection bias (Wang and Han, 2021). However, such a situation is different from the scenario where the original outcome GWAS is missing people from the same underlying population (birth cohorts) as those included, some of whom have already died from the instrument and some of whom have already died from the outcome or a competing risk of the outcome, as shown in Figures 1C,D.

In this study, as an extension of negative control outcomes, we advance the use of control exposures to validate MR estimates that might be susceptible to such selection bias. We focus on plausible causal structures relevant to MR studies and illustrate how to validate MR estimates using control exposures through a real example investigating the potential association of transferrin with stroke (including ischemic and cardioembolic stroke). This association is thought to be particularly vulnerable to selection bias, especially among older populations, because transferrin affects survival and stroke is open to competing risk from IHD (Schooling et al., 2020; Yang et al., 2021). We further discuss the criteria for choosing the control exposures and the limitations of this approach.

Figures 1C,D show DAGs for MR with selection bias caused by sample selection. In the presence of competing risks (Figure 1C), the selected samples may have a lower risk of developing the phenotype [e.g., the outcome (D)] because the GWAS is missing people with genetic vulnerability to earlier death and people who have died from a disease that shares causes (e.g., U) with the phenotype. As such, the backdoor pathway directly linking G_E1 to D will be reopened in the selected samples if the instruments affect survival, i.e., have allele frequencies that differ from the underlying population (e.g., birth cohort). This situation violates the IV3 assumption and distorts MR estimates, which can attenuate or reverse the true association or create a spurious association. The small effect sizes of genetic associations (Park et al., 2011; Global Burden of Disease, 2020) make them particularly vulnerable to perturbation by such bias (Schooling et al., 2020). In the absence of competing risks (Figure 1D), the phenotype (e.g., D) risk and instruments’ frequencies may vary because of selecting on genetic instruments and outcome, which generates unrecoverable selection bias.

To clearly illustrate the data-generating process underlying selection bias due to missing people from the original birth cohorts who formed the underlying population through death before study recruitment, we conducted extensive simulation studies. Details are presented in the Supplementary Material. Briefly, we induced selection bias by selecting study participants as survivors to study recruitment. We assumed that the survival of the underlying population was influenced by the genetic instruments G_E1, exposure E₁, outcome D, confounder C of the exposure–outcome association, or the unmeasured confounder U mediated by competing risks CR. We used the relative hazard (i.e., hazard ratio) per-unit change in either G_E1, E₁, C, D, or U to quantify their effects on the survival, as shown in Supplementary Figure S1. As such, the impact of selection bias induced by the survival status of the underlying population until study recruitment was governed by hazard ratio of per-unit change in either G_E1, E₁, C, D, or U. Then, we induced selection bias in two-sample MR by having instruments determining survival to recruitment and outcome of interest affecting survival to recruitment. Details of the simulation study are in the Supplementary Material, along with the corresponding R scripts.

Figure 3 and Supplementary Figure S1 show the impact of selection bias arising from selecting samples conditioning on genetic instruments G and outcome D, with no effects of either exposure E₁ or the shared confounder U mediated by competing risks on survival of the underlying population (i.e., birth cohort) based on simulation studies. More details have been presented in Supplementary Material S1. As expected, selecting samples conditioning on genetic instruments G and outcome D of interest induces selection bias, with its impacts varying depending on the relative hazard of G and D on survival of the underlying population. Given summary statistics obtained from the original exposure and outcome GWASs, it seems not easy to recover the true causal estimate from the observed MR estimates in two-sample MR settings due to the essence of missing people before the recruitment of the original GWASs.

Up to 11 genetic instruments were used for transferrin (mean concentration 2.1 g/L and SD 0.43 g/L), 7 instruments for transferrin saturation (mean percentage 29.9% and SD 11.0%), and 5 instruments for iron status (mean concentration 18.4 μmol/L and SD 5.6 μmol/L). The F-statistics of instruments for transferrin ranged from 32.4 to 1,296.1, for transferrin saturation ranged from 35.6 to 808.5, and for iron status was 37.8 to 346.7, suggesting weak instrument bias to be less likely.

Figure 4 shows the scatter plot of the estimated effects of genetically predicted higher transferrin versus higher transferrin saturation (A), higher transferrin versus higher iron status (B), and higher transferrin saturation versus higher iron status (C) on stroke (including ischemic and cardioembolic stroke) and longevity, with full details presented in Supplementary Table S3. Genetically predicted higher transferrin was associated with a lower risk of stroke (Figures 4A,B), although these protective effects did not reach nominal significance (p < 0.05). Conversely, genetically predicted higher transferrin saturation was nominally associated with higher risk of stroke (Figures 4A,C). Such results suggest that the observed transferrin–stroke association is open to selection bias, possibly due to the missing people from the original GWAS of stroke because they died before recruitment from the genetic predictors of iron, an iron-related condition, stroke, or a competing risk of stroke, which attenuated the true association (Figure 2).

In addition, as expected (Gill et al., 2018; Daghlas and Gill, 2021), genetically predicted higher iron status was associated with increased stroke and reduced longevity, as shown in Figures 4B,C and Supplementary Table S3. Finally, the consistent effects of higher transferrin saturation and higher iron status on stroke and longevity further triangulated our conclusions. Even if selection bias exists, its impact on the transferrin saturation–stroke and iron status–stroke associations would be limited or at least could not reverse the observed associations or biased them to the null. These results support the advantages of using control exposures.

This paper advances the use of control exposures based on subject matter knowledge in MR studies to triangulate the estimated causal effects vulnerable to selection bias. The potential mechanisms underlying selection bias in MR lies in the re-opened backdoor pathway from genetic instruments to the outcome of interest in the selected samples. It violates the IV3 assumption and distorts the MR estimates. The applied example demonstrates that MR is vulnerable to selection bias because of missing data from sample selection (Figures 1, 3), which is unlikely to be missing at random, so requires modeling of the missing data process to recover the estimates (Mohan and Pearl, 2021). Our proposal provides a valuable approach to assessing credible MR estimates in the presence of selection bias from selection of survivors.

Furthermore, the control exposures introduced in the proposal inherit properties similar to those of negative or positive control exposures used in the conventional observational studies but provide a more intuitive and clinically meaningful interpretation of the estimated effects (Lipsitch et al., 2010; Shi et al., 2020; Sanderson et al., 2021). Choosing antagonists, decoys, or exposures with similar biological activity as the control exposures based on subject matter knowledge may facilitate its application in MR studies. Systematic selection bias distorting both the exposure–outcome and control exposure–outcome associations, in a similar or even the same way, may exist, resulting in inconclusive or misleading conclusions. However, an additional or a validated control exposure with a clear association with the outcome provides another tool to triangulate the estimated effects. Notably, it is possible to use a single control exposure in the proposal solely to validate the MR estimates, especially when E₁, E₂, and E₃ are selected from different GWASs.

Despite the strengths of the proposal in validating MR estimates, limitations exist. First, the proposal only detects potential selection bias but fails to address it. The impact of selection bias on summary statistics obtained from the original GWAS might vary due to the small fraction of heritability explained by genetic variants and the small effect size of the genetic associations (Greenland, 2003; Freedman et al., 2004; Park et al., 2011; Schooling, 2019). Thus, the proposal might fail to detect its small effect on MR estimates. Nonetheless, routinely applying control exposures still adds more credibility to MR estimates. Second, the proposal inherits properties of the conventional MR; limitations such as the stringent instrumental assumptions remain (Davey Smith and Ebrahim, 2003; Smith and Ebrahim, 2004; Lawlor et al., 2008). However, recent advances in MR provide more tools to alleviate or even eliminate these limitations (Ye et al., 2019; Zhao et al., 2020; Liu et al., 2021). Third, choosing control exposures that have the same potential selection bias sources as the exposure–outcome association of interest or a clear association with the outcome might be difficult in practice, further limiting its application.

Routinely using control exposures in MR studies provides a helpful tool to validate estimated causal effects that are vulnerable to potential selection bias in the selected samples.