For debate:
It is well recognized that failure to follow up and include in the
analysis all patients randomised in a clinical trial is a potential
source of bias. Furthermore, analysis by `intention to treat' implies
that patient should not be excluded from analysis after randomisation.
While some studies have achieved remarkable rates of follow-up,
attrition is common, particularly when the outcomes can only be
obtained from the patient (for example, report of symptoms), rather
than from other sources (for example, medical records or death
certificates).
I spend a lot of time trying to perform meta-analysis on randomised
trials of smoking cessation. Losses to follow-up are often quite large
in such trials. Commonly, those lost to follow-up are included in the
analysis, assuming `conservatively' that they were treatment failures
(continued to smoke), a convention we have followed when entering data
into meta-analysis. However this assumption is only conservative under
certain conditions, and may in fact exaggerate treatment effects if
losses to follow-up are greater in the control arm.
For example, Slama and colleagues (Tobacco Control 1995) in a study of
advice from family doctors randomised 2199 to receive advice and 929
to act as controls. 706 (32%) of the intervention group and 409 (44%)
of the control group were lost to follow-up. For the binary outcome,
smoking or not smoking, an odds ratio (intervention/control) can be
calculated. If the drop-outs are excluded from the analysis this is
42x520/1493x5 = 2.94. If all drop-outs are counted as continued
smokers, then the odds ratio becomes 42x 929/2199x5 = 3.55.
In an interesting recent paper on this topic, (Shadish WR, Hu X,
Glaser RR, Kownacki R, Wong S. A method for exploring the effects of
attrition in randomized experiments with dichotomous outcomes.
Psychological Methods 1998,3: 3-22) , Shadish and colleagues suggested
that two further odds ratios should be calculated: 1. Under the
extreme conservative assumption that all the losses to follow-up in
the control arm quit smoking, and all those in the treatment arm
continued to smoke 2. Under the optimistic assumption that all those
lost to follow-up in the intervention group quit and none of those in
the control group. If both of these are greater than 1, then the
suggested benefit of treatment is robust.
However, this criterion is met in few smoking cessation studies. For
example, in the Slama study, the `worst case' odds ratio = 0.024 and
the `best case' = 93! Shadish goes on to suggest that odds ratios be
generated for all possible combinations of outcomes in the drop-outs
(which in the example I have used would be 706 x 409 = 288754). A p
value can then be obtained for the observed odds ratio. This seems
attractive, though impossible to do without a specially written
programme.
It is my impression that few RCT's report a quantitative estimate of
how their results might be affected by attrition bias. Do others have
views on the most appropriate way of handling this problem?
Tim Lancaster
Division of Public Health and Primary Care,
Institute of Health Sciences,
Old Road,
Headington,
Oxford
OX3 7LF
Tel 01865 226997
Fax 01865 227137
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