The absence of association between anorexia nervosa and smoking: converging evidence across two studies

Anorexia nervosa (AN) is an eating disorder characterised by persistent food restriction and an abnormal attitude towards eating and weight (e.g., distorted self-perception, fear of eating and weight-gain; [1]). AN has one of the highest mortality rates of all psychiatric disorders [2], and severe effects on physical and mental health that last beyond weight recovery [3‐6]. Amongst adults with AN, tobacco smoking and nicotine dependence are reported as elevated as compared with healthy controls (HC; [7‐9]). Amongst adolescents, it is commonly reported that weight concern, one of the core psychological symptoms of AN, is associated with increased risk of current and future smoking [10, 11]. There is some evidence to support nicotine suppressing appetite and increasing metabolism [12], and individuals with AN cite motivators for smoking to include weight-loss/avoidance of eating [13]. Such observations lend support to the proposal that AN pathology, (or the drive to maintain a low body weight), causes smoking (e.g. [14]).

The observed association between AN and smoking could, however, be explained by causal effects in the reverse direction. For example, appetite suppressing effects of smoking may instigate food restriction and weight loss that is experienced as reinforcing by those with a vulnerability to AN, prompting further and excessive engagement in restrictive eating behaviour (e.g. [15‐18]). Equally, smoking may increase AN risk by affecting brain structure and function (e.g. [19, 20]). Finally, AN and smoking might not be causally related at all and could instead share causal risk factors: confounding could induce an association between the two.

Smoking causes various noncommunicable diseases and is the leading cause of preventable death globally [21]. Understanding how smoking and AN development are associated may thus inform mechanisms underpinning the disproportionate burden of disease amongst psychiatric patients [22], as well as AN aetiology. Though previous studies have explored the co-occurrence of AN and smoking, they have been limited in their ability to make causal inferences. To our knowledge, no study has probed the longitudinal association between AN and smoking. Yet, to establish that one phenotype (a) causes another (b) it is necessary, though not sufficient, to demonstrate that phenotype (a) precedes phenotype (b). Furthermore, observational research (both cross-sectional and longitudinal) is prone to bias arising from confounding and reverse causation. Confidence in outcomes of observational research may be strengthened by triangulation with outcomes of studies of differing design, given that each design will be vulnerable to different sources of error [23].

In the current investigation we study the association between AN and smoking using two designs that have not yet been applied to this research question. In Study One, we conduct observational longitudinal analyses addressing bidirectional associations between AN and smoking in a large adolescent population sample. The adolescent period is particularly relevant for addressing questions surrounding temporal patterns of smoking and AN occurrence, given AN onset is typically between the ages of 15 and 19 [24], and smoking also typically starts during adolescence [25]. To date, and to our knowledge, no study has specifically studied smoking behaviour amongst adolescents with AN or observational associations between smoking and AN in an adolescent cohort.

Study Two adopts a two-sample Mendelian randomization (MR [26]) design. MR employs genetic variants as instruments for an exposure of interest, minimising bias due to confounding and reverse causation [27]. Both AN and smoking behaviours are moderately heritable, with twin studies suggesting 50–60% of the variance in AN and 44–75% of the variance in smoking behaviours is explained by genetic factors [28, 29]. A reasonable proportion is explained by common genetic variants, with single nucleotide polymorphism (SNP) heritability estimates of 11–17% for AN and up to 8% for smoking behaviours [30, 31]. Current genetic instruments for AN and smoking explain 1.7% and 2.3% of the variance, respectively [30, 31]. Given the different sources of bias from each study design, consistent inferences across Studies One and Two would thus increase confidence in the validity of the results. Given previous findings concerning the presence and motivators of smoking behaviour amongst AN, and support for nicotine affecting body weight and neural function in ways that could conceivably increase risk for AN, we hypothesised causal effects in both directions.

This research explored the association between smoking behaviour and AN. Findings were triangulated across two study designs (longitudinal observational, and MR), which were subject to different sources of bias, to improve the accuracy of inferences. It was hypothesised that associations consistent with bi-directional causal effects between smoking and AN would be observed. Contrary to hypotheses, we found no clear evidence to support longitudinal associations between AN and smoking behaviour. Outcomes of MR analyses were consistent, producing no evidence to support causal associations between AN and smoking.

Prospective associations between smoking behaviour and AN have not to our knowledge been explored previously. The absence of association of AN with either smoking initiation or heaviness is novel and informative, though does conflict with prior reports that elevated AN psychopathology (i.e. weight concern) is associated with increased risk of smoking in adolescent populations [11, 50]. The discrepancy may be explained by AN diagnosis and AN psychopathology being different phenotypes, with a population high in weight concern being more diverse, and likely less harm avoidant, than individuals with a diagnosis of AN. The lack of evidence for a cross-sectional association between AN and smoking contrasts with previous case–control studies that have reported an increased prevalence of smoking [8] or nicotine dependence [7] in AN relative to HC. Differences in sample demographic characteristics between studies could account for differing findings. The age of our sample was younger than that of studies previously described, and it is possible associations strengthen in adulthood. Indeed smoking prevalence is more common amongst adults with AN as compared to adolescents with AN [51]. Alternatively, the fact we adjusted for various confounders in the analysis, while statistical control in prior studies has been somewhat limited [51], may explain conflicting findings. Consistent with this explanation, there was evidence to support cross-sectional associations between AN and smoking heaviness in unadjusted data analyses. The associations identified in prior studies may reflect the existence of shared risk factors for AN and smoking that were not accounted for in the analysis.

In Study 2, there was also no clear evidence for a causal effect of AN on smoking behaviour, or of causal effects of smoking behaviour on AN. Given the MR design of Study Two reduces bias from confounding, this outcome supports the proposal that previously reported cross-sectional associations between AN and smoking (e.g. [7, 8]) may to some extent be explained by operation of a third unmeasured factor. One plausible shared risk factor is negative affect, comprising anxious and depressed mood, for which the worry we adjusted for in multivariable observational analyses may serve as a proxy [52]. Negative affect has been associated with subsequent initiation of smoking and smoking heaviness [53], as well as with AN [54, 55]. Evidence supports causal effects of negative affect on smoking in smokers (e.g. [56‐58] and on disordered eating in AN (e.g. [59, 60]). Furthermore, smokers report reductions in negative affect following smoking [61, 62] and individuals with AN report reductions in negative affect following engagement in disordered eating [60]. Smoking and restrictive eating may thus reflect an underlying proneness to negative affect, with both behaviours functioning as maladaptive coping strategies.

The existence of shared risk factors might be expected to play out in longitudinal as well as cross-sectional associations. However, effects of such risk factors could be proximal, and levels of the risk factors dynamic over time. In addition, shared risk factors of smoking and AN are no doubt common to a number of other health risk behaviours and psychiatric disorders [63‐66]. An underlying vulnerability may be expressed in various different ways, which may change over time with the developmental context. This would further increase the dependency of detecting associations between smoking and AN on the timing of assessment. Targeting those factors that causally increase risk for both substance use and disordered eating in prevention efforts (e.g. [67]) comprises a cost-effective strategy for improving public health. A priority area for future research is to confirm potential shared causal risk factors as such, and to develop novel prevention interventions accordingly. Notably, this strategy is likely to be more useful when considering a wider collection of health behaviours and psychiatric symptoms.

In each of the studies we took several measures to increase the accuracy of effect estimates and conclusions. In Study One, associations were assessed across multiple waves of data, and missing covariate data were imputed, to maximise use of available AN and smoking variable observations. Analyses were conducted with imputed, maximally available and complete case data. Point estimates and corresponding inferences were generally consistent across analyses, strengthening confidence in conclusions. We adjusted our analyses to account for effects of potential confounding factors, took the clustered nature of repeated measures data into account and considered mechanisms surrounding data missingness, to promote unbiased inferences. The large sample size increases reliability and validity of resulting conclusions. In Study Two, we used a Mendelian randomisation design, which reduces bias from confounding and reverse causation, to strengthen causal inference [26]. The MR method is particularly powerful for phenotypes such as smoking and AN diagnosis, which are either impossible or unethical to randomise, meaning effects of these exposures cannot be investigated using a randomised control trial. Confounding can be reintroduced via pleiotropic pathways. We conducted multiple sensitivity analyses to determine bias arising from pleiotropy and judged the strength of evidence generated from the MR analyses by looking for consistent effect estimates across multiple methods. Generally, effect estimates were close to zero, or confidence intervals were wide, enhancing confidence in the conclusion that there is no strong statistical evidence for an effect in either direction.

Each of the two studies had limitations. In Study One, AN diagnoses were assigned using a population assessment strategy, rather than resulting from clinical interviews or clinician evaluations. Measurement error may have acted to dampen associations when AN was the exposure and reduce statistical power when AN was the outcome [68]. Residual confounding is probable, given it is unlikely all confounders were sufficiently accounted for in the analysis [69]. The number of AN cases was low in the prospective investigation (Study One), rendering analyses with the AN outcome vulnerable to rare events bias, and analyses with the AN exposure vulnerable to data sparsity effects, particularly in adjusted analyses. AN disproportionately affects females, potentially increasing issues with data sparsity when covarying for gender in our analyses. Reassuringly, however, coefficients and standard errors of the observational analyses did not show signs of the effect size inflation that is symptomatic of rare events/data sparsity bias.

Study Two is not vulnerable to these sources of bias;, however, alternative causes of error are plausible. The largest source of bias in MR studies is pleiotropic effects. Though we used MR Egger to formally quantify such effects (finding no indication of bias due to pleiotropy), these estimates should be interpreted with caution due to variance of the SNP-exposure associations [43]. We did not have an AN sample stratified by smoking status and, therefore, were unable to assess distinct effects between AN and smoking duration/heaviness/cessation, which may have prevented us from detecting true associations in MR analyses. However, the lifetime smoking measure indexes smoking heaviness in unstratified samples, and results of analyses using this measure showed no evidence for causal effects. MR analyses with the AN exposure are likely to be very underpowered, since only 7 genome-wide significant SNPs were available for use as AN instruments, and power in MR analyses is primarily dictated by the variance in exposure explained by the SNP instruments [70]. Though a sensitivity analysis with a relaxed p-value threshold for instrument identification still resulted in no clear evidence for causal effects, we note that estimates will be biased towards the null when using weaker instruments (less strongly associated with the exposure) [71]. It is also important to note that MR estimates lifetime effects, and, therefore, is not sensitive to particular critical windows or developmental stages. However, this makes MR complementary to longitudinal observational analyses focusing on particular life stages, as in Study One, in which we examined associations between AN and smoking during the adolescent period. An assumption of the two-sample MR method is that the exposure and outcome GWAS are conducted in homogenous populations, with heterogeneity leading to possible bias [72]. The GWAS included individuals with European ancestry only; however, there was a large sex discrepancy, with around 54% of participants in both smoking GWAS being female, compared to an estimated 97% of participants in the AN GWAS. Genetic variants for AN previously identified in a female-only GWAS did predict AN risk in an all male sample [31], suggesting that these variants should still be valid instruments for AN in a smoking GWAS of mixed sex. Finally, two-sample MR can be biased by sample overlap in the exposure and outcome samples [73]. UK Biobank was included in GSCAN, and the population in which the composite smoking instrument was constructed, and UK Biobank also provided 768 cases and 3065 controls to the AN GWAS. Sample overlap is unlikely to have affected the interpretation of our results given it was small. Furthermore, such overlap would bias results towards the confounded observational estimate (and away from the null; [73]), yet there was no evidence for an association across analyses.

As the sources of bias differed across studies, the consistent results across the two studies allow for greater confidence that AN and smoking are not causally related, as compared to inferences based on outcomes of only one of the studies. However, it is possible for biases to have acted in the same way across the two studies (i.e. towards the null), which would undermine the strength of triangulating evidence across investigations of differing design. Across both studies we were not able to probe differential associations of smoking behaviour between AN subtypes. In the observational study this would have resulted in data sparsity and low power given the small number of AN cases. Use of summary GWAS data in MR analyses did not allow for subtype identification and separate group analyses either, though it has been reported that the genetic basis of AN does not vary by subtype [31]—consistent with the high level of cross over from restrictive to binge-purge AN [74]. However, there is some evidence to suggest prior associations identified between AN and smoking are driven by greater smoking in binge-purge AN, with reduced likelihood of smoking in restrictive AN [7, 75, 76]. Effect modification by subtype could therefore have prevented detection of true causal effects in both studies. MR analyses with the smoking initiation exposure, and prospective analyses of the association between smoking initiation and subsequent AN development, lacked power to detect small effects (these analyses had less than 80% power to detect an OR below 1.45 and 1.8, respectively), which could equally result in outcomes of Studies One and Two leading to the same wrong conclusion. True effects may well be smaller than expectations arising from prior cross-sectional findings, given confounding in cross-sectional studies is likely. As AN psychopathology in nonclinical populations is associated with a greater likelihood of smoking (e.g., [50, 75]), the effects of AN per se on smoking risk may be particularly small.

Across two complementary studies, each with particular strengths, limitations and sources of bias, there was no evidence for causal effects between AN and smoking. In unadjusted analyses, AN was cross-sectionally associated with greater heaviness of smoking, potentially indicating the existence of shared risk factors for smoking and AN pathology. Elucidating such shared risk factors may highlight novel targets of prevention efforts able to simultaneously address health risk behaviour and psychiatric symptoms, to reduce the overall burden of ill-health in the population. Low power and effect modification by AN subtype could have masked meaningful relationships in the current study and should be considered in future investigations.