In addition to placing prior distributions on the coefficients in expression (1), we also placed a prior distribution on the unknown variable smpre. The exposure model accomplishes this by expressing the probability of reporting periconceptional smoking when asked during early pregnancy as a function of the predictors in zi′. This model allowed us to account for differences in smoking probability among various groups of women.
Here, ω is a vector of the effects of the predictors in zi′, and ω0 is the intercept. The outcome is reported smoking status in the periconceptional period, which is not commonly observed in studies. This makes it difficult to use the results of previous studies to inform priors for parameter estimates. We placed N(0,1) priors on coefficients in this model, implying we are 95% certain the true OR relating any exposure with reported periconceptional smoking status lies between, roughly, OR = 1/7 and OR = 7. Additional prior specifications are considered in the eAppendix (available in the online version of this article).
The last of the 3 regression models is the measurement model, in which the probability that a woman reports periconceptional smoking after delivery, smipost, depends on her smoking status during the periconceptional period and whether her child was diagnosed with a cleft. Notice that because smipost may depend on the outcome, we are allowing for differential misclassification:
The parameters in expression (3) correspond to the sensitivity and false-positive rate (FPR, or 1-specificity) of reported maternal smoking among case and control mothers. The probability of reporting smoking after delivery is separated into mutually exclusive components depending on case/control status and maternal report of smoking: α0 is the sensitivity of reported smoking among control mothers, α1 is the FPR among control mothers, α2 is the sensitivity among case mothers, and α3 is the FPR among case mothers. We used the exposure model and the measurement model to impute values of smpre in a manner analogous to that used with missing data techniques; we then used those imputed values to estimate the effect of periconceptional smoking on children's OFC risk. The data, however, contain little information about the 4 parameters in the measurement model, so prior specification for these parameters can have a large impact on inference.
To examine the impact that misclassification might have had on the effect of smoking and clefting risk, we implemented 4 models that specify α0, α1, α2, and α3 in the measurement model by using different prior distributions. Model 1, our reference model, is based on the assumption that the periconceptional smoking status reported by women after their delivery is the same as what they would have reported had they been asked during their periconceptional period. In terms of the measurement model specified previously, this translates into the assumption that α0 = α2 = 1, and (1 – α1) = (1 – α3) = 1. With the parameters in expression (3) fixed at smipre = smpost, the outcome model (1) simplifies to:
Combined with the priors for β0, β1, and θ outlined previously, this is a standard Bayesian logistic regression model.
Model 2 is based on the assumption that women's smoking was differentially misclassified but the amount of the misclassification is known with certainty. The corrections made in analyses based on this model are roughly equivalent to common corrections for misclassification seen in the epidemiologic literature.40 It has been shown that such an approach can be highly sensitive to even small discrepancies between the assumed and actual values of sensitivity and specificity.38,41 There are few data on the reporting of maternal smoking during pregnancy that could help us quantify the sensitivity and specificity of self-reported smoking data for case and control subjects. We are aware of no studies that provide information on accuracy of smoking reporting among mothers of infants with clefts and only 1 study that provides information on accuracy of smoking reporting among mothers of infants with congenital malformations.29 In that study, conducted in the Netherlands in 1978 and 1979, women were asked about their smoking status at approximately the 18th week of gestation and again following delivery. Congenital malformations were found in 40 infants, allowing rather imprecise estimates of sensitivity and specificity to be generated for case mothers, whereas 2320 infants were born at term without any malformation, allowing more precise estimates of sensitivity and specificity among control mothers. The parameters we specified in the measurement model (3) were equal to the maximum likelihood estimates of sensitivity and FPR (among case and control mothers) estimated from data reported in this article: α0 = 0.91, α1 = 0.06, α2 = 0.94, and α3 = 0.09.
Model 3 is based on the assumption that the sensitivities and FPRs used in the measurement model (2) are unknown (rather than constant and known with certainty) and reflects concern about using even slightly inaccurate values of sensitivity and specificity to correct for misclassification. Because sensitivities and FPRs must fall between 0 and 1, a natural choice for a prior distribution is a beta distribution, which gives support only to values between 0 and 1. The beta distribution is defined by 2 parameters, b1 and b2, and has a mean of b1/(b1 + b2). The parameters b1 and b2 can be interpreted as the number of “successes” and “failures” in some trial, respectively. For sensitivities, b1 is the number of women who report smoking after delivery and in early pregnancy and b2 is the number of women who report not smoking after delivery but report smoking in early pregnancy. For FPRs, b1 is the number of women who report smoking after delivery but not during early pregnancy, and b2 is the number of women who report not smoking after delivery and not smoking during early pregnancy. The prior distributions for sensitivity and FPR among case and control mothers that we use in Model 3 are shown in Figure 2. Because of the difference in the number of case and control mothers in the validation study (40 versus 2320), the estimates of sensitivity (mean = 0.91, 95% CI = 0.89–0.93) and FPR (mean = 0.06, 95% CI = 0.04–0.07) among control mothers were more precise than the estimates of sensitivity (mean = 0.94, 95% CI = 0.81–1.0) and FPR (mean = 0.09, 95% CI = 0.01–0.24) among case mothers. We present analyses in the eAppendix using different prior specifications.
In Models (1), (2), and (3), we use data from previous studies on maternal reporting of smoking to impute values of a woman's smoking status during the periconceptional period. The gold standard used in the previous studies was self-report of smoking during early pregnancy. Additional reporting bias is possible, however, and self-report during early pregnancy may not be an accurate description of a woman's true smoking status. In particular, women who smoke during early pregnancy may underreport their smoking. This may be the reason for the surprisingly low specificities observed in previous research29: women who reported not smoking during early pregnancy but who did report smoking later during their pregnancy may have truly smoked during the periconceptional period but did not accurately report it. In this scenario, as depicted in Figure 3, an additional measurement model must be specified for the probability of reporting smoking during the periconceptional period given true smoking status (arrow F). Previous studies have examined the validity of women's self-reported smoking status during pregnancy by comparing their reported status with levels of cotinine found in their blood or urine.42–45 Two of these studies collected data in the 1960s and 2 in the 1990s. Because estimates of sensitivity and specificity in the 4 studies were very similar, we pooled the data from the 4 studies to generate a single estimate. The pooled FPR estimate indicates that women who were truly not smokers rarely reported that they were (mean = 0.02, 95% CI = 0.02–0.03), whereas the pooled sensitivity estimate indicates that some women who did smoke reported that they did not (mean = 0.92, 95% CI = 0.91–0.93). In Model 4 we combine the outcome, exposure, and measurement models we defined in Model 3 with an additional measurement model that corrects for response bias:
Here, γ0 is the sensitivity of reported smoking, and γ1 is the FPR. In contrast to the measurement model in expression (3), this one is nondifferential. We placed beta priors on the sensitivity and FPR in this model, with parameters corresponding to the pooled estimates described previously.
We performed a number of sensitivity analyses to judge the influence of our prior assumptions in the exposure and measurement models. We also performed additional analyses examining the effect of maternal smoking on isolated clefts (those having no additional major defects) and multiple defects (major unrelated defects in 2 or more different organ systems); these are shown in the eAppendix. We fit all models using Markov chain Monte Carlo (MCMC) algorithms in OpenBUGS and R.46,47 The code needed to fit these models is also shown in the eAppendix. MCMC algorithms were run for 20,000 iterations, with the first 1000 iterations excluded as a burn-in period. We ran multiple chains from different initial positions and visually examined trace plots to monitor convergence. Following the burn-in period, the iterations of the MCMC algorithm are random draws from the posterior distributions of interest. The median of these random draws was exponentiated to obtain the posterior OR of interest, and the 2.5th and 97.5th percentiles of the random draws were exponentiated to obtain posterior credible intervals.
The National Birth Defects Prevention Study enrolled 6909 infants who met our case and control definitions (4874 controls, 1323 with CL/P, and 712 with CPO). As shown in Table 2, control mothers were less likely to be non-Hispanic white and less likely to report a family history of clefts than mothers of infants with either CL/P or CPO. The observed ORs in Table 2 are consistent with the prior specification in Table 1.
The 4 models, run separately for CL/P and CPO, converged relatively quickly. Posterior ORs and 95% credible intervals are shown in Table 3. Model 1, which did not correct for exposure misclassification, indicated a slight increased risk for CL/P and CPO among children of mothers who reported periconceptional smoking. Estimates from Model 2, which corrected for misclassification but treated the sensitivity and specificity of misclassification as known with certainty were shifted toward the null. Estimates from Model 3, which treated the sensitivity and specificity as unknown, had wider credible intervals and showed a greater association between maternal smoking and CL/P risk than the estimates from Model 2, but a similar association between maternal smoking and CPO risk. Estimates from Model 4, which incorporated additional information on self-reported smoking relative to cotinine levels were similar to those from Model 3.
Results of sensitivity analyses shown in the eAppendix indicated that varying the assumptions regarding prior distributions of coefficients in the outcome or exposure model did not result in any substantial changes to inference. Varying the prior distributions for the FPR and sensitivity resulted in wider posterior credible intervals but little change in posterior ORs.
After accounting for smoking misclassification, we found an increased risk for CL/P among infants of mothers who smoked during the periconceptional period. The effect of maternal periconceptional smoking on children's CPO risk was less clear, with a posterior effect near the null but imprecise credible intervals.
Model 1 was a standard Bayesian logistic regression that assumed perfect sensitivity and specificity of maternal reporting. This model produced effect estimates of periconceptional maternal smoking on children's risk for CL/P and CPO that were very similar to meta-analysis estimates by Little et al.25 The large size of our dataset ensured estimates were robust to prior specification for this model (see eAppendix); our results using the first Bayesian model were virtually identical to the frequentist results reported by Honein et al.20 Model 2, which corrected for maternal reporting bias by treating sensitivity and specificity as known constants, resulted in smaller estimated effects. The sensitivities and specificities we specified would be expected to produce differential misclassification away from the null, so corrected estimates will naturally move toward the null. In these data, the combination of lower specificity among cases than controls resulted in a relative surplus of infants categorized as exposed cases.
Model 3, which allowed sensitivities and specificities to be unknown, produced posterior effect estimates that were larger than those produced by Model 2. When uncertainty in maternal reporting was accounted for in this model, there was still evidence that periconceptional smoking had an effect on CL/P; however, there was far less evidence of an effect of smoking on CPO.
It is interesting to note that Model 3 resulted in different estimates for CL/P than Model 2. Because Model 2 treats sensitivities and specificities as known with certainty, the posterior values for the sensitivity and specificity parameters will always be identical to their priors: no amount of data can change them. Sensitivities and specificities in Model 3, on the other hand, adapt in light of the data. Many of the variables in Z are predictive of maternal smoking, and these variables were used to impute the unobserved periconceptional smoking status for each woman. The sensitivity and specificity parameters were then updated in light of how well these imputed variables corresponded to observed smoking status. Among mothers of infants with CL/P, the data imply smoking is reported more accurately than our prior indicated. In fact, the posterior distribution for specificity among cases had a mean of 0.96 and 95% credible intervals (0.93–0.99) that did not include the fixed estimate of 0.91 used in Model 2. The results for CPO were somewhat similar to those in Model 2 because, due to the smaller sample size of CPO cases, the posterior distribution of sensitivity and specificity was not very different from the priors and still centered near the values used for correction in Model 2. Estimates from Model 4 are largely unchanged relative to Model 3. In some of the additional analyses presented in the eAppendix, the additional uncertainty incorporated in Model 4 produces somewhat more imprecise credible intervals. The effect of maternal smoking on children's risk for CL/P produced by Model 4 was quite similar to that found in one cohort study, although estimates of the association between smoking and CPO risk were somewhat different.48 A more recent cohort study with very little misclassification of maternal smoking, published while our paper was in press, found very similar results to ours.49
The study we used to help quantify the sensitivity and specificity of self-reported smoking status among case and control mothers is not ideal (nor is the additional study we include in the eAppendix). It was not conducted in a population similar to that participating in National Birth Defects Prevention Study or collected in the same decade. Given the divergent and changing attitudes toward smoking over time and in different countries, it is not clear how well the sensitivities and specificities in the study we used mimic those that would have been found in our source population. Additionally, the time between delivery and the postpregnancy interview was typically shorter in that study than in our data. For these reasons, Models 3 and 4 (which assume the effect estimate is not known with certainty) are particularly appealing. A typical analysis of these data would assume perfect recall (as in Model 1), and underestimate our true uncertainty of the effect of smoking on risk of clefts. Our ability to introduce uncertainty about the accuracy of recall and have that uncertainty reflected in the posterior ORs and credible intervals is a major benefit of this approach. Furthermore, we assumed that all variables in our model, other than smoking, were measured without error; we did not consider other types of errors that may also bias results. For example, we cannot rule out selection bias as a possible source of error if, for instance, case mothers who smoked during the periconceptional period were more likely to enroll than nonsmoking case mothers, or if maternal smoking had a selective impact on embryonic and fetal survival. The models we propose, however, could easily be adapted to incorporate this information if there were reasonable prior values.
Whether periconceptional smoking has an effect on the risk of facial clefts is not likely to be solved with further case-control studies, at least not without significant modification in how and what data are collected. In any event, extensive simulation studies would be needed to evaluate power in complicated settings such as the one we considered, although results and some formulae are provided for simpler settings of exposure misclassification in Gustafson.50 The estimates from Model 1 (in which misclassification is ignored) are precise; however, the width of the credible intervals about the estimates nearly doubled when we accounted for misclassification. The imprecision of these effects is partially due to our lack of information about the validity of maternal self-report of smoking during pregnancy; future studies focusing on the validity of maternal reporting (especially in relation to case status) would have a large impact in decreasing the uncertainty of these effects.
We have focused on a particularly interesting example, the effect of periconceptional maternal smoking on risk of facial clefts. Recall bias or differential misclassification represents a common concern in birth defects and pediatric epidemiology, but this scenario has broader applicability.
Results of numerous case-control studies have shown that maternal smoking during pregnancy is associated with an increased risk for of clefts; however, the interpretation of these effects is difficult due to the possible presence of reporting bias. The models we present correct for reporting bias and lend some support to the hypothesis that periconceptional smoking is associated with an increased risk for CL/P. The results concerning CPO are more mixed with little overall evidence of effect but less precise estimates.
These methods have broad applicability in other misclassification settings as well. The general strategy of specifying an exposure, measurement, and outcome model based on a DAG and jointly estimating modes in BUGS should be transportable to other studies. Clearly, misclassification can occur in prospective as well as retrospective studies and some alterations of the DAG may be necessary for these studies. For instance, arrow B in Figures 1 and 2 would not typically be present when the exposure measurement is made prior to the occurrence of the outcome. However, only minor modification of the code provided in the appendix would be necessary to run these models in other settings. Care should always be taken when specifying prior distributions. Insufficiently informative priors in either the exposure model or the measurement model may lead to poorly behaved MCMC algorithms. Generally speaking, the further the sensitivities and specificities are from 1.0, the greater the difference between the crude and adjusted OR could be. Furthermore, if a great deal is known about the sensitivity and specificity of recall, the results of Model 3 (or Model 4) will not differ much from the results of Model 2. Conversely, as the uncertainty regarding recall increases, Models 3 and 4 (which propagate that uncertainty through the model) will be particularly appealing.
We thank Joanna Smith for programming support and Ruby Nguyen and David Dunson for helpful comments on an earlier version of this paper.
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