Re: Association between psychological distress and mortality: individual participant pooled analysis of 10 prospective cohort studies
Low Distress and Death: Scary Headlines from Confounded Data
A lot of scary headlines and misinformation in the media could have been avoided with more modest claims and better epidemiology in a recent BMJ article concerning the mortality associated with low distress, as well as in its accompanying editorial and BMJ generated press release.
Efforts to relate psychological distress to negative physical health outcomes including mortality have a long and frustrating history. Distress has so many antecedent and concurrent associations that determining whether its relation to outcomes like mortality are spurious and due to its association with antecedents often proves impossible. Distress is related to a host of personal and socioeconomic disadvantages and health problems and health related impairments that can reasonably be expected to affect future morbidity and mortality. Sometimes these alternative explanations of the association between distress and sickness and death can seem to be ruled out in multivariate analyses. But as George Davey Smith and others have repeatedly shown, such multivariate analyses also can produce counterintuitive and nonsensical results, including findings that distress is associated with better health and longevity when particular statistical controls are introduced and others left out. Whenever we examine relations between distress and health, we need to remind ourselves that association is not causality and that is often difficult or impossible to infer public health implications from observational data. We also need to remind ourselves that to rely on multivariate statistics to settle issues of causality in observational studies often requires untenable assumptions about having a model that distinguishes between confounds and simple covariates and that we have identified all relevant confounds and measured them with great precision. Otherwise we can assume that residual confounding and other forms of spuriousness will rear their ugly heads.
The authors make unwarranted assumptions about what is represented by low scores on the Brief Symptom Inventory. Even when scores are above the established cutpoints, most high scores do not represent psychiatric disorders. Assumption about the validity and substantive interpretation of scores above established cutpoints do not generalize to low scores. Low scores may variously represent moderate endorsement of a number of items that are not symptoms of psychopathology and may even represent diffuse physical health complaints. Alternatively, low scores may represent stronger endorsement of a small number of items such as sleep disturbance that may be related to other factors, which turn may directly contribute to morbidity and mortality. The meaning of low scores is much more ambiguous than the meaning of high scores.
The authors could have discouraged misinterpretation if they presented their results in terms of differences in absolute risk. Readers could thereby see that we are talking about small differences. Even as they are presented, results are not in the range that we can consider as having public health implications. Instead, they are well within the range that could expected with residual confounding and the failure to specify and adequately measure the full range of confounding variables. This basic criticism is aside from the question of not knowing what public health interventions could banish such low levels of distress. The authors have indeed assembled a large data set of individual level data, but such large data sets carry the risk of overinterpreting small effects of a spurious nature.
The authors put too much effort into trying to defend their results concerning distress and cancer. First, it is incorrect to state, as they did, that the association between distress and cancer death remained in the fully adjusted model because the confidence interval included .99. More importantly however, the authors accepted uncritically the findings of a meta-analysis concerning the influence of psychological factors on cancer incidence, progression and outcome. That meta-analysis would have yielded only trivial effects for psychological factors if it had appropriately excluded the discredited data of Eysenck and Grossarth-Maticek. Whereas most hazard ratios clustered around 1.0, the data of Eysenck and Grossarth-Maticek yielded hazard ratios in the implausible realm of 23.8 to 74.2 . These data have been widely discredited  and Eysenck is now known to have received large undisclosed payments from lawyers for American tobacco companies to publish these data. Regardless, even without this knowledge, the extreme deviation from other data would 'have justified exclusion of these data from these studies as outliers. Aside from all the other issues posed by this BMJ article, it represents yet another instance of the persistent influence of suspect data on our understanding of the association between psychological variables and cancer. Let's keep these data out of the literature, but let’s also stick to more modest claims and make a better effort to explain ambiguous results to lay audiences if press releases are sent out.
1.Chida, Y., Hamer, M., Wardle, J. & Steptoe, A. Do stress-related psychosocial factors contribute to cancer incidence and survival? Nature Clinical Practice Oncology. 2008. 5, 466–475.
2.Van der Ploeg, H.M. . What a wonderful world it would be: a reanalysis of some of the work of Grossarth-Maticek. Psychological Inquiry. 1991. 2, 280-285.
3.Coyne, J. C., Ranchor, A. V., & Palmer, S. C. Meta-analysis of stress-related factors in cancer. Nature Reviews Clinical Oncology, 2010. 7(5).
Competing interests: No competing interests