The ALSPAC cohort (23–25) recruited 14,541 pregnant women resident in and around the City of Bristol, South West UK, with expected dates of delivery 01/04/1991 to 31/12/1992. There were 14,203 unique mothers initially enrolled in the study. Mothers invited partners to complete questionnaires at the start of the study and 12,113 partners have provided data to the study. Please note that the ALSPAC study website contains details of all the data that are available through a fully searchable data dictionary (http://www.bristol.ac.uk/alspac/researchers/our-data/).

The unit of analysis for this investigation is the index offspring of the pregnancies. Eligibility criteria for children in this investigation were (1) surviving to 1 year of age, (2) being a singleton pregnancy, (3) not having a known cause of ID (see (7) for derivation of known causes of ID), (4) not having withdrawn consent by the time of analysis, and (5) having an NHS number so that ALSPAC data could be linked to outcome information on the UK Secure eResearch Platform. Children with a known cause of ID were excluded, as this is a group in which ID is likely regardless of exposure to maternal smoking during pregnancy. This left a total sample size of 13,479 children (see Figure 1 for a flowchart of exclusions).

Binary (yes/no) and count (number of cigarettes per day) variables for maternal and partner smoking during pregnancy were derived from questionnaire responses intended to be complete at 18 weeks’ gestation (actual gestation at completion varied). Detailed description of the questionnaires, derivation process, and time of completion is provided in the Supplementary Methods . We use the term partner as opposed to paternal throughout to acknowledge that in ALSPAC, the mother’s partner may not be the biological father of the child.

The derivation of a multiple-sourced variable for ID has been described in detail elsewhere (7). Briefly, data linkage was employed to combine information on IQ scores assessed by ALSPAC fieldworkers when the children were age 8 and 15, diagnoses of ID using Read (26, 27) and ICD (6) codes in general practitioner (GP) and hospital episode statistic (HES) records, statements of special educational needs for cognitive and learning needs (28) from school census records, and free text information recorded in questionnaires by participants and their guardians (including mothers, partners, and other primary carers) across the lifetime of the study. A child was indicated as having ID if two or more of the sources indicated having ID. Known causes of ID used in the eligibility criteria (including genetic, metabolic, or chromosomal abnormalities associated with ID) were also identified from GP, HES, and free text information.

The variables used as covariates in models were the following: child sex assigned at birth, maternal age at the time of birth, maternal parity, maternal depressive symptoms at 18 weeks’ gestation, maternal alcohol use recorded at 18 weeks’ gestation, maternal reported financial difficulties recorded at 32 weeks’ gestation, maternal education recorded at 32 weeks’ gestation, and maternal occupational class recorded at 32 weeks’ gestation. Detailed description of variable derivations can be found in the Supplementary Methods .

All analyses were performed using R version 3.5.3 (29).

To assess the likelihood of bias from missing data, we compared the prevalence/means of exposure, outcome, confounders, and auxiliary variables between those included in the sample and those excluded. We further performed logistic regression of being included in complete record analysis on each variable without adjustment. Complete record analysis has been shown to be biased when the probability of missing data is jointly dependent on both the exposure and the outcome for logistic regression (32).

All observational analyses and negative control analyses were conducted as complete records analyses and repeated using multiple imputation. Multiple imputation was implemented to reduce bias and improve efficiency (33). Previous work has shown that, provided the data meet the missing at random (MAR) assumption, multiple imputation can produce unbiased results even at large proportions of missing data (34). Data were imputed using fully conditional specification (35, 36) carried out using the R package “mice” (37) with 100 imputations. The exposure, outcome, and all maternal and partner covariates were included in the imputation model to maintain consistency between the imputation model and the most complex analysis model (the fully adjusted negative control model). Each variable was included as a predictor of all other variables.

Auxiliary variables were also included in the imputation model in order to improve the plausibility of the MAR assumption (36). We included two auxiliary variables for socioeconomic status as the analysis model variables for this (financial difficulties, education, and occupation) were often missing. The auxiliary variables were home ownership status and present maternal marital status, both recorded at approximately 6 weeks’ gestation. Further details of the multiple imputation procedure and auxiliary variables are detailed in the Supplementary Methods .

We report the fraction of missing information (FMI) for the exposure coefficient. The FMI is a parameter-specific measure that quantifies the loss of information due to missing data while accounting for information recovered by multiple imputation (38, 39). Values of FMI range between 0 and 1 with values close to 1 indicating that observed data in the imputation model does not provide much information about the missing data.

The results of the observational analyses for both binary and count exposure are presented in Table 2 . Both complete records analysis and multiple imputation analysis found no association between the binary measure of maternal smoking during pregnancy and offspring odds of ID. Models that were unadjusted and adjusted for confounders were all consistent with no effect (OR for fully adjusted model = 0.83; 95% CI = 0.48–1.44). Results for the count exposure showed a 1.29-fold increased odds of ID per 10 cigarettes smoked per day in pregnancy (95%CI = 0.82–2.01) in the unadjusted model. This association was attenuated somewhat after adjusting for maternal characteristics and attenuated substantially towards the null following adjustment for socioeconomic characteristics (OR for the fully adjusted model = 1.01; 95%CI = 0.63–1.60). Results from multiple imputation analyses were consistent with those from complete records analysis. Values of FMI were close to 0, indicating that we did not lose substantial information on the exposure-outcome association to missing data.

Table 3 shows that in complete records analyses, the effect estimates for the binary exposure suggested that maternal smoking was associated with reduced odds of ID in offspring (fully adjusted OR = 0.69; 95% CI = 0.26–1.82) whereas partner smoking was associated with increased odds (fully adjusted OR = 1.18; 95% CI = 0.54–2.56). It is important to note that both effect estimates are consistent with the null and consistent with each other, providing evidence against a causal effect of smoking in pregnancy on offspring risk of ID. Multiple imputation analyses that account for missing data brought both maternal and partner effect estimates closer to the null and closer to each other.

Results for the count exposure show a greater OR per 10 cigarettes smoked per day for partner smoking than maternal smoking (unadjusted maternal OR and 95% CI = 1.20, 0.54–2.66; unadjusted partner OR and 95% CI = 1.40, 0.93–2.10). These estimates were attenuated towards the null following adjustment for confounders (fully adjusted maternal OR and 95% CI = 1.09, 0.47–2.52; fully adjusted partner OR and 95% CI = 1.27, 0.81–1.97). As with the binary exposure, these estimates are consistent with the null and with each other providing evidence against a causal effect of maternal smoking in pregnancy. Multiple imputation analyses again brought the estimates closer to the null and closer together.

Prior work has suggested an increased risk of ID following prenatal exposure to maternal smoking during pregnancy. A meta-analysis (12) of two case–control studies (8, 9) and two prospective birth cohort studies (10, 11) suggested a small increased risk (OR = 1.10 95% CI 1.06–1.15), although the included studies did not adequately account for confounding and may also suffer from selection and recall bias. The estimate from our unadjusted model using a binary exposure is close to the meta-analyzed value. Adjusted OR estimates of studies not included in the meta-analysis range from 1.27 (95% CI = 1.19–1.34) (14) to 1.35 (95% CI = 1.28–1.42) (16). These effect estimates are greater in magnitude than the effects estimated in the current study but do overlap with the confidence intervals we have produced owing in part to our smaller sample size and larger standard errors.

The results of the present study and the suggestion of no causal effect by our negative control analyses are consistent with other studies using causal inference methods (16, 17), namely, the exposure discordant sibling design, which accounts for unmeasured genetic and environmental confounding shared between siblings. The result of the present study therefore provides further evidence to suggest that observational associations between maternal smoking in pregnancy and offspring risk of ID reflect unmeasured or residual confounding. Each of these studies may be susceptible to their own biases; for example, sibling designs are susceptible to bias from non-shared confounding between siblings and carryover effects where the outcome or exposure of one pregnancy influences the exposure status in following pregnancies, although in both cases bias is more likely to be away from the null. The negative control assumes that bias from all sources (confounding, selection, and measurement error) are equivalent for the maternal and partner exposure. This assumption may not hold perfectly in our study as there were differing relationships between the maternal and partner exposure variables and missing data. In spite of this, both maternal and partner effect estimates were close to the null following adjustment for confounding suggesting a lack of association or causal effect of smoking in pregnancy on offspring risk of ID.

We have used a pregnancy cohort with prospectively collected data which will reduce the chance of differential measurement error in the exposure (recall bias). The ALSPAC cohort contains information on an extensive range of maternal and partner characteristics, which has enabled us to adjust for a wide set of confounding variables which were also prospectively collected. Despite this, we likely did not fully account for confounding in our adjustment set, in part due to the difficult nature of characterizing socioeconomic position, and therefore, residual and unmeasured confounding is possible. To overcome this, we implemented a causal inference technique, the negative control design, to try to account for bias from unmeasured confounding, selection, and measurement error. We acknowledge that these biasing structures for maternal and partner smoking may not overlap perfectly. The negative control design accounts for some level of genetic confounding as both mother and father contribute 50% of their genetics to the genetics of the child; comparing maternal with paternal smoking effects means that each effect should be confounded by genetics to a similar extent. However, not all partners in this study may have been the biological father of the child and so the partner smoking effect may suffer from less genetic confounding than the maternal smoking effect. It is also possible that mothers in the study underreported how much they smoked during pregnancy to a greater extent than partners due to differences in social pressures and desirability (40). This could result in a greater bias towards the null for the maternal effect than the partner effect.

The ALSPAC cohort has a relatively small sample size compared with other studies using national registers. This means that we have more uncertainty in our estimates than some prior studies. It is important in the context of a lack of statistical power to remember that absence of evidence is not equivalent to evidence of absence; however, given that these results agree with our prior findings for a lack of causal effect, we are encouraged in our conclusions. Furthermore, ALSPAC overrepresents mothers with White ethnicity than the UK population as a whole, due in large part to the demographics of the eligible population in the catchment area at the time, and so may be less generalizable than studies using national registers.

ALSPAC is also afflicted by socioeconomic and health patterning in attrition (41). Our study has been strengthened by our use of data linkage to healthcare and education records to reduce the quantity of missing data in the outcome. This will have improved the statistical efficiency of our estimates (thereby reducing uncertainty) and likely reduced bias in analyses by reducing the dependency of the probability of missing data in the outcome on the underlying value of the outcome itself (32). We further accounted for missing data in the exposure and confounders variables using multiple imputation, improving statistical efficiency. We found close estimates between complete records analysis and MI, but it is important to note that this does not provide evidence that estimates are unbiased by missing data as both complete records and multiple imputation analysis could be biased to a similar extent if the MAR assumption was not met. We used auxiliary variables to improve the plausibility that data in exposure and confounding variables was MAR.