possible. As an example, we present the protocol for an idealised version of Trolle [15]. (i) (ii) (iii) (iv) Population: Non-sensitised Rhesus negative women deliv- ered of Rhesus positive babies at Kolding Hospital, Denmark Intervention: Dose of 1500 IU anti-D immunoglobulin given at 28 weeks’ gestation, in addition to control antenatal care Control: Dose of at least 1000 IU anti-D immunoglobulin given postpartum and anti-D offered after potentially sensitising events during pregnancy. Outcome: Sensitisation at 10 months postpartum This protocol describes the intended population, intervention strategy, control strategy and outcome in the Trolle study, according to the published study report [15]. The actual study differed from the imagined idealised study in several respects, which will be discussed later in the paper. To identify internal biases in the 10 studies of the effectiveness of RAADP, we compared each study against its idealised version. An internal bias checklist was completed for each study. This entailed answering a series of questions about potential sources of bias, and summarising relevant details extracted from the original papers. Following the methodology of Turner et al. [19], we considered the following five categories of internal bias: biases caused by differences between intervention and control groups at baseline (‘‘selection bias’’); biases related to lack of blinding of participants or caregivers (‘‘performance bias’’); biases caused by exclusions and drop-outs (‘‘attrition bias’’); biases related to measurement of the outcome (‘‘outcome bias’’) and additional biases (‘‘other bias suspected’’). To identify external biases, we compared the idealised versions of the RAADP studies against the target setting. An external bias checklist was completed for each study. We considered the following four categories of external bias: biases caused by differences between the idealised study population and target population of non-sensitised pregnant Rhesus negative women in the UK (‘‘population bias’’); differences between the study and target interventions (‘‘intervention bias’’); differences between the study and target control strategies (‘‘control bias’’); and differences between the outcome measured in the study and the target outcome, sensitisation which would affect a subsequent pregnancy (‘‘outcome bias’’). Bias assessment Internal biases were assessed by four assessors with quantitative expertise (three biostatisticians and one obstetrician), and external biases were assessed separately by four assessors selected for their knowledge of anti-D prophylaxis. At the elicitation meetings, the assessors discussed each study in turn and reviewed the bias checklist, while discussing any queries and resolving misunder- standings. For each bias, assessors agreed whether the bias would change only the magnitude of the intervention effect (a proportional bias) or whether it could change the direction of effect (an additive bias). After the group discussion, the assessors independently gave their opinions on the magnitude (and uncertainty) of each bias in each study, by marking ranges on bias elicitation scales (Figure 1). Opinions about the size and uncertainty in the biases were marked using 67% intervals, such that the assessor believed the true bias was twice as likely to lie inside rather than outside this range. For example, if the assessor believed that a study with historical controls was likely to be subject to a major additive internal selection bias favouring Effectiveness of Antenatal Anti-D Prophylaxis RAADP, then a 67% interval might be indicated as 0.4 to 0.8 on the left-hand side of the upper scale in Figure 1. If the assessor believed that a study of primigravidae was almost entirely relevant to all non-sensitised pregnant women, then an interval of 0.9 to 1/ 0.9 might be indicated for a proportional external population bias on the lower scale. Bias-adjusted meta-analysis For each assessor, we calculated means and variances for total bias in each study, for additive and proportional biases separately. These were used to adjust the study effect estimates and standard errors for bias, while acknowledging the uncertainty about the extent of bias [19]. For each study, results were pooled across assessors by taking the medians of the assessors’ adjusted estimates and standard errors, in order to obtain the opinion of a ‘‘typical’’ assessor [20]. Finally, a conventional random-effects meta-analysis was used to combine the bias-adjusted results across studies. Statistical heterogeneity was assessed using the I2 statistic [21], which gives the percentage of variation between the study estimates attributable to true between-study heterogeneity rather than random variation; 0% indicates no heterogeneity. Analysis comparing different dose regimens In a meta-regression analysis, we used the data available from the RAADP studies to inform us about the relative effectiveness of three anti-D dose regimens which were of particular interest in the second NICE appraisal. These are the three licensed anti-D treatments: 500 IU at 28 and 34 weeks; 1500 IU at 28–30 weeks; 1250 IU at 28 and 34 weeks. Four of the RAADP studies evaluated the effectiveness of the first of these [10,12–14], but no studies have evaluated either of the latter two treatments exactly as specified. In principle, it would be possible to use the available study data to compare the effectiveness of giving 500 IU at 28 and 34 weeks with the effectiveness of giving 1500 IU at 28 weeks (evaluated in three studies [7,8,15]) or 1500 IU at 28 and 34 weeks (evaluated in one study [6]). However, the small number of studies means that differences between dose regimens would be very imprecisely estimated. Subgroup analyses comparing the effects of different doses cannot provide any conclusive findings in this data set. We therefore elicited opinion on the relative effectiveness of all RAADP treatment regimens of relevance, comprising the five treatments evaluated in one or more studies and the two treatments which are licensed but as yet unevaluated. For each treatment regimen, four assessors with knowledge of anti-D prophylaxis were asked to provide numerical 67% ranges to describe their belief and uncertainty about the effectiveness of this treatment relative to an imagined optimally effective treatment (i.e. one which would prevent all sensitisations during pregnancy). Assessors were asked to take into account the half-life of prophylactic anti-D (approximately 3 weeks), the minimum circulating level required to provide protection against sensitisa- tion, and anticipated compliance with each treatment regime. Pilgrim et al. [5] noted that compliance may be greater for a single-dose regimen for logistical reasons, but also that a two-dose regimen offers an opportunity to reduce the risk somewhat if the first appointment is missed. Values on the elicitation scale for relative effectiveness ranged from 0 for a treatment no better than control to 1 for an optimally effective treatment. A meta-regression analysis [22] was performed to estimate the association between the measure of relative effectiveness (as a predictor measured with uncertainty) and the observed effectiveness of the five treatments on which data are available. The observed odds ratios were first adjusted for all PLoS ONE | www.plosone.org 3 February 2012 | Volume 7 | Issue 2 | e30711