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• W2972989495 abstract "The last two decades of epidemiologic research have included a rapid adoption of instrumental variable (IV) methods for leveraging natural experiments in the estimation of causal effects.1,2 Recently, epidemiologists have doubled down on such approaches, using not just one but several proposed IVs simultaneously. The practice of judiciously combining information from several potential IVs may be a case in which the whole is greater than the sum of its parts; it may also be a case in which previously recognized problems with methods based on a single IV are compounded. This issue of EPIDEMIOLOGY includes a review of recent methodological advancements for Mendelian randomization studies proposing multiple genetic variants as IVs.3 These newer methods have several noteworthy advantages, including the ability to address the very real concerns regarding power, weak IV biases, and imperfect IVs that are ubiquitous and often intractable in Mendelian randomization studies with single genetic variants.3–6 Here, we take a step back to remind ourselves what we can and cannot learn about causal effects from observational studies with multiple proposed IVs. In short, we ask: can we see the forest for the IVs? Throughout, our goal is to estimate causal effects. This diverges from Burgess and colleagues’ primary goal of testing,3 but aligns with this journal’s reporting guidelines emphasizing effect size over statistical significance and related recent dialogues.7,8 For didactic purposes, discussion of confidence intervals appears in the eAppendix (https://links.lww.com/EDE/B113). ESTIMATING CAUSAL EFFECTS USING A SINGLE PROPOSED INSTRUMENT Before considering the full forest, we begin with a brief review of what can be achieved with a single IV. Suppose we want to estimate the “global” average causal effect of a dichotomous treatment A on a dichotomous outcome Y on the risk difference scale, and we assume that a dichotomous variable Z1 is a true IV (i.e., Z1 is associated with A, causes the outcome only through A, and shares no causes with Y). Identification further requires a homogeneity condition.9–11 Assuming no additive effect modification by Z1 among the treated and untreated, the standard IV ratio, (E[Y|Z1 = 1] − E[Y|Z1 = 0])/(E[A|Z1 = 1] − E[A|Z1 = 0]), identifies this effect. For example, consider our toy dataset with a proposed IV (Z1), treatment (A), and outcome (Y). (The data are summarized in the Table, and the data-generating procedure and complete code are provided in the eAppendix; https://links.lww.com/EDE/B113). The above ratio is (0.35–0.36)/(0.54–0.44) = −10%.TABLE: Proportion of Study Population (N = 10,000,000) Who Are Treated (A = 1) and Who Experience the Outcome (Y = 1) by Levels of the Four Proposed IVs (Z 1, Z 2, Z 3, Z 4)If homogeneity is not plausible (as is the case in many research settings),10–12 another option is to target a “local” average causal effect within a subset of the study population.10,13 Assuming Z1 causes A and a monotonicity condition, for example, the same IV ratio identifies the effect in individuals who would have been treated had Z1 = 1 but not otherwise. Note this effect pertains to a generally unidentifiable subgroup (because we do not observe individual treatment levels under both levels of Z1). We can repeat the computations above using three other dichotomous proposed IVs in our dataset (Z2, Z3, Z4), obtaining different estimates (Figure 1). The next question to ask is what can be done if we consider the proposed IVs simultaneously?FIGURE 1: Forest plot of bounds and point estimates for the “global” average causal effect computed under various sets of assumed IVs and further assumptions. Data are generated such that the true causal risk difference is 0.3 or 30% (dotted line). Gray indicates that the method requires one or more homogeneity conditions for valid identification; black indicates that the method does not require a homogeneity condition for valid (partial or point) identification.ESTIMATING CAUSAL EFFECTS USING MULTIPLE PROPOSED INSTRUMENTS The four estimates using the standard IV ratio range from strong negative to strong positive effect sizes. When considering “local” effects, triangulating or pooling such estimates is suboptimal because the definitions of “local” effects are IV dependent.12,14 For example, if all assumptions hold, the effect computed using Z1 (−10%) pertains to a subpopulation defined with respect to counterfactual treatment levels under Z1, while the effect computed using Z2 (10%) pertains to a subpopulation defined with respect to counterfactual treatment levels under Z2. As such, the discrepancies between the four estimates could be because of sampling variability, because some assumption(s) do not hold, or because the estimates are targeting effects in different subpopulations. For this reason, from here on we restrict attention to the “global” average causal effect. If all four proposed IVs were valid and the requisite homogeneity conditions all held, then any differences between our four estimates is due to sampling variability. Thus, the wide range of our four estimates from a large study suggests at least some of these assumptions do not hold (Burgess et al.3 provide further review of over-identification tests to assess this empirically). Unfortunately, we do not know which assumptions are violated, and therefore cannot conclude which (if any) of our estimates is valid. As reviewed by Burgess et al., there are IV-based methods to estimate the effect while relaxing some of these assumptions. Although the details vary depending on the specific approach, penalization- and median-based methods typically require that a subset (e.g., >50%) of the IV ratios are valid, implying that a subset of the proposed IVs are valid and their respective homogeneity conditions are satisfied.5,6 Egger regression, on the other hand, allows all four estimates to be biased, but the method as developed requires that biases are due to specific violations of the second IV condition and that the magnitudes of biases are not associated with the IV ratio denominators.4 We obtain negative, null, and positive estimates when applying variations of these robust methods to our data. At this point, a responsible epidemiologist may write up these results as inconclusive and suggest that further research (perhaps leveraging different data and assumptions) is warranted. However, we have not yet exhausted all IV-based methods in our epidemiologic toolbox. We turn next to bounding. BOUNDING CAUSAL EFFECTS USING A SINGLE PROPOSED INSTRUMENT To obtain a point estimate for the effect generally requires an IV and homogeneity, but the effect can be bounded under the IV conditions alone.9,15,16 That is, we can compute lower and upper limits for the effect assuming that Z1 is an IV but without assuming homogeneity. In practice, such bounds are often quite wide. In our data, for example, assuming Z1 is an IV implies the effect is between −28% and 64%. BOUNDING CAUSAL EFFECTS USING MULTIPLE PROPOSED INSTRUMENTS While bounds based on a single IV are wide, using multiple proposed IVs can afford opportunities to triangulate and tighten bounds, as formalized in the eAppendix (https://links.lww.com/EDE/B113). As a first step, consider the four bounds computed using the four proposed IVs separately. Under the assumptions that Z1, Z2, Z3, and Z4 are all (marginally) IVs, then logically the effect must lie within all four bounds and therefore their intersection: 3% to 59%. If instead we assume that only a subset of the proposed IVs are valid (as is the benefit of penalization- and median-based methods, but without requiring homogeneity), then the effect must lie within some, but not necessarily all, of these bounds. For example, assuming a single proposed IV is valid (but we do not know which one), the effect is bounded by −28% and 67%. Likewise, based on prior knowledge of the probable validity of each IV, we could triangulate bounds under various further permutations of assumed IVs. Under the assumptions encoded in the causal diagram in Figure 2, the four proposed IVs are not just four IVs that marginally satisfy the IV conditions: they also jointly satisfy the IV conditions, in that we can combine them into a single IV with 24 = 16 levels. Assuming the IVs jointly satisfy the IV conditions that allows substantially better use of the full observed data distribution: we can apply a more general expression for bounds.17 In our particular example, the lower and upper bounds computed under a joint IV model are equal and therefore the effect is identified as 30%, which is exactly the true average causal effect in these data.FIGURE 2: Causal diagram depicting four causal IVs (Z 1, Z 2, Z 3, Z 4), treatment (A), outcome (Y), and unmeasured confounders (U).The data example was selected to illustrate a setting for which it is difficult to make sense of the collection of (here, biased) results from methods requiring homogeneity conditions, while bounding approaches proved collectively informative (and, here, valid). An explanation of the cultivated example is provided in the eAppendix (https://links.lww.com/EDE/B113). Note, unknown to us as analysts, Figure 2 indeed depicted the true data-generating procedure. The eAppendix (https://links.lww.com/EDE/B113) includes further discussion of more realistic settings, including when some of the proposed IVs are indeed invalid. EXTENSIONS AND APPLICABILITY OF BOUNDING APPROACHES USING MULTIPLE PROPOSED INSTRUMENTS A bounding perspective lends itself to several immediate extensions. We can combine marginally computed bounds readily to study other causal parameters (e.g., the causal risk ratio),15,18 to settings with continuous outcomes,16 to two-sample designs (and therefore some forms of summary data),19 and to approaches based on different expressions of the IV conditions or combining the IV conditions with certain additional assumptions.9,15–20 The jointly computed bounds are from results presented by Richardson and Robins17 for any dichotomous treatment, dichotomous outcome, and set of IVs that collectively take k levels and jointly satisfy the IV conditions. In practice, however, there may not be subjects with all k possible combinations of the IVs: for our four proposed dichotomous IVs, we had k = 24 = 16 strata, but with a larger set of proposed IVs this becomes unwieldy in realistic sample sizes. Another consideration is whether, in a given study, the proposed IVs are likely to satisfy the IV conditions marginally, jointly, or both. As described in the eAppendix (https://links.lww.com/EDE/B113), drawing one or more causal diagrams may help address this query and inform the choice of appropriate bounding approaches for a given study.21 Unlike the data example considered by Burgess et al., here we considered dichotomous treatments. This was chosen for illustrative purposes, as estimating effects of continuous treatments necessarily requires specifying the dose–response model (i.e., a parametric approach is unavoidable for continuous treatments).22 Most Mendelian randomization estimators require a linear dose–response in conjunction with other parametric conditions. When linearity is unrealistic, investigators could consider bounding with a discretized continuous treatment. This approach, however, can introduce its own bias via invalidating the IV conditions.23,24 While this may be perceived as limiting the applicability of a bounding mindset, it also underscores the inherent difficulties with and reliance on parametric assumptions when estimating causal effects of continuous treatments. Unfortunately, the reviewed methods all fail to capture key practical issues with estimating causal effects using Mendelian randomization, namely ill-defined or time-varying treatments. These issues are not unique to Mendelian randomization—indeed, Mendelian randomization studies are often motivated by confusing results in non IV observational studies—but their repercussions on IV-based estimates receive limited attention. Without addressing these concerns, however, increasing the number or improving the type of proposed IVs will not yield better estimates, let alone tests, of causal effects. In other words, advanced methods alone cannot save us from imprecise questions. THE VIEW FROM THE TREETOPS For studies with multiple proposed IVs, Burgess et al. advocated presenting sensitivity analyses and effect estimates based on several methods that rely on different assumptions. In addition to the methods they reviewed, conducting one or several bounding procedures may be of especial interest when effect heterogeneity is expected. Another advantage of bounding is that nested assumption sets can be readily considered, thereby illuminating our reliance on each added assumption.18 Thus, even if the bounds computing in realistic settings with multiple proposed IVs end up being wide in practice, such bounds nonetheless provide insight into just how reliant causal inferences are on specific assumptions.25 Given all this, when feasible and appropriate, presenting bounds and point estimates computed under complementary sets of IV-type assumptions can help us understand the “forest” of information in our data and our assumptions; however, in practice visualizing the “forest” may reveal how little we know rather than how much. ABOUT THE AUTHOR SONJA SWANSON is an Assistant Professor in the Department of Epidemiology, Erasmus MC. Her methodological research focuses on developing, improving, and increasing the transparency of causal inference methods in epidemiology. ACKNOWLEDGMENT I thank Vanessa Didelez, James Robins, and Ryan Seals for helpful comments on earlier versions of this manuscript." @default.
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