We thank Drs Sleight and Brophy for their challenging editorial on our ReoPro cost-effectiveness study. The editorial raises several important issues to which we would like to reply. In general, we agree that publication bias can exist with cost-effectiveness studies but remind our critics that this is a potential problem with all scientific research. Further, we accept that the long term outcomes of patients given ReoPro were unclear as we had only six month efficacy data. That was why we performed a two-step analysis with cost-effectiveness data from the pivotal study presented first, followed by an analysis to explore the impact on long term outcomes.

The trial based analysis is not flawed in its scope or because of selection bias. The EPIC trial was concerned with specific indications that were not fully examined in the other two studies mentioned (CAPTURE and EPILOG). Further, no accounting error has been made. The modelled analysis aimed to explore the long term outcomes with ReoPro and indicated cost-effective event free survival and overall survival. Three year follow up data of EPIC patients have since been published and have shown significant improvement in event free survival and, despite limited statistical power for individual end points, a trend to reduced mortality (odds ratio 0.78; 95% confidence intervals (CI) 0.53 to 1.14).

We defend the focus on the EPIC trial and clarify that the results of the other clinical trials were considered at the time of writing (see “clinical effectiveness”). However, the aim was to examine cost-effectiveness in the EPIC defined high risk population.1 The EPILOG study essentially assessed an “all comers population” that excluded patients who were eligible for the EPIC study2 except patients with “EPIC eligible” morphological characteristics. The CAPTURE study assessed the use of ReoPro to stabilise refractory unstable angina patients before PTCA, administering a 24 hour treatment and stopping the ReoPro infusion soon after the PTCA.3 Consequently, these two studies were not similar to EPIC. Despite this, we mentioned in the article that these studies confirm the level of treatment effect. In addition, only the EPIC trial collected detailed resource use information available for analysis that made a trial based analysis possible. Safety was improved in EPILOG with more refined techniques in administration than seen in EPIC. Therefore, the main issue from the other studies was one of an improved risk:benefit ratio, which was discussed.

The value of reduced PTCA as a part of the composite clinical end point is questioned as the baseline level of PTCA may be too high. PTCA was recorded as an urgent intervention for a recurrent ischaemic event and was strictly defined. We contend that urgent PTCA is a relevant efficacy end point and appropriate for a trial based evaluation. Funders and clinicians can make up their own minds as to the value for money gained from the trial based evaluation. Further, PTCA was credibly measured within a large double blind randomised trial. Indeed, one of the best epidemiological studies in this area by Weintraubet al in the USA4 confirms that restenosis leads to greater myocardial infarction, repeat PTCA, and CABG. Although mortality was not reduced, this is linked to a high rate of repeat PTCA within the first year of restenosis (75%). Consequently, such high rates of PTCA may prevent death after restenosis. We included epidemiological studies with intervention rates closer to that for Australia but raised the findings of Weintraub et al.

The applicability of the EPIC trial is necessarily limited to the procedures used and the patients studied, which can be said of any major clinical trial. Indeed, the use of stents may have changed the role of ReoPro but this question is being addressed in the EPILOG stent substudy. Data on the use of stents in high risk patients are limited and the onus is perhaps on our critics to present relevant data. We caution against subgroup analysis given its reduced statistical power and comparability between groups, and remind readers that the best estimate of treatment effect comes from the overall effect from a well conducted trial. This is why we were cautious of interim results indicating similar benefit in non-high risk elective PTCA (that is, a much wider group) and await further research.

Consequently, it is surprising that our critics do not accept the results of a large randomised trial on efficacy at six months in favour of an assessment of what might happen if the trial was run again. Interestingly, three year follow up results have since been published.5 While remembering that the EPIC trial was not powered to look for a mortality benefit, outcomes (as measured by the composite end point) were significantly improved up to three years after treatment and an increasing trend to reduced mortality exists (odds ratio 0.78; 95% CI 0.53 to 1.14).

The results of the model are presented separately to make the analysis transparent. As indicated in the Australian cost-effectiveness guidelines, a modelled economic evaluation should follow on from a trial based analysis so that the impact on results can be assessed.6 Necessarily, much of the technical detail could not be published in an article of this nature for which content and word limit is imposed. We admit that a limited number of cohort studies were included in the modelled analysis but this resulted mainly from including studies that assessed the long term impact of restenosis post-PTCA.

There is no accounting error in the calculation of the cost-effectiveness ratios. As is standard practice, the cumulative cost is related to the cumulative benefit over the six month period. For those who are interested, a standard text is recommended.7On average, patients on ReoPro incurred an additional cost of $1054 by six months and experienced an 8.1% reduction in the composite end point. Health events can occur in the denominator as “effectiveness” as well as in the numerator as “cost”. There is no sense in removing the risk reduction during the initial hospitalisation from the six month cost-effectiveness ratio.

Finally, the “back of the envelope analysis” presented in the editorial seems to go against our critics’ central message for good quality and comprehensive data analysis. We contend that our “envelope” was considerably larger but appreciate their “enthusiasm”.

In conclusion, the trial based analysis presented considers a particular indication, does not suffer from selection bias, and has no accounting error. The applicability of the trial is indeed limited to its design (as with any trial) and issues such as the impact of stenting are not yet known (as was highlighted). We presented a modelled evaluation to assess the impact on long term outcomes. The need for a modelled approach requires a balance between its scope and foundations. The separate presentation of the trial based and model based analyses can assist the reader in appraising each. Since our modelling exercise, event free survival at three years has been confirmed in the EPIC follow up study with a trend to improved survival. This suggests to us that the “totality of evidence” is somewhat different.