A comment and a question.
1. Seems like this problem is a good reason to apply the "quality
filter" of 80% followup for inclusion in your meta-analyses. Or perhaps
the problem is whether you can even do meta-analyses in areas where
followup is uniformly poor.
2. "Dumb question": Aren't your calculations RR's and not OR's given
they are prospective? Is this a nomenclature problem or am I missing
some major concept?
Thanks.
Katherine Schneider, MD
On Wed, 16 Sep 1998, Tim Lancaster wrote:
> 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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