1 Newcastle, UK 2 York, UK
Editor The conclusion reached by Stone and colleagues1 is correct as far as it goes, but is misleading when considering the question they sought to answer: does the addition of dopexamine to intraoperative volume expansion confer added benefit? The conclusion reached was that they were unable to demonstrate such a benefit. This is not surprising given the study design, and should not be interpreted as meaning that a benefit does not exist. It is possible that the authors accept this, as they raise many of the criticisms themselves in their discussion. However, the fact that the paper has been given a prominent position in the BJA and is accompanied by an uncritical editorial,2 runs the risk of lending more weight to the conclusions than the study merits.
The study was powered to have an 85% chance of showing a halving of postoperative morbidity. With their sample size, any smaller benefit would not achieve significance. It is my belief that anaesthetists, surgeons, and their patients would be grateful for a technique that reduced the risk of morbidity by even 5 or 10%: lack of proof of 50% risk reduction does not mean an intervention has no merit. The previous study from the York group3 was perhaps surprising in that the benefits of dopexamine group over the epinephrine group seemed to be so large.
Unfortunately, Stones study has other problems. The treatment group was not evenly matched with the control group, as the authors acknowledge. There were more than twice the number of patients with COPD and diabetes in the treatment group than in the control group, more than three times the incidence of ischaemic heart disease, and four times the incidence of peripheral vascular disease. Thus, the treatment group would have been expected to have more postoperative problems than the control group: in fact they had less (36/50 compared with 57/50). In an attempt to allow for the different risks posed by the treatment and control groups, the authors have compared the actual incidence of morbidity with that predicted by the POSSUM score. While this is a valiant effort, it is unfortunate that the mortality in their study patients was far lower than that predicted by POSSUM, demonstrating that POSSUM is not a valid predictor of outcome in their patient group. Further, the dose of dopexamine used was half that of the starting dose recommended by the manufacturer. This study does not tell us anything about outcomes when using a conventional, larger dose.
Had the study been sufficiently powered to detect, say, a 20% reduction in morbidity, and the groups had been evenly matched for co-morbidity, then it may have been possible to draw valid conclusions. Finding the answers to such questions is notoriously difficult, and demonstrates the limitations of randomized controlled trials, the designs of which are constrained by what is practical. It is important not to accept uncritically the conclusions of limited or poorly designed studies, which may then be extrapolated beyond the conditions imposed by the study protocol. I am surprised that the editorial accompanying the paper2 failed to make this point.
P. J. M. Bayly
Newcastle, UK
EditorWe thank Dr Bayly for his interest in our paper. As he points out, in our discussion we have addressed the problems with study design, particularly the power of the study and the failure of the randomization process to give two evenly matched groups. The power analysis was based on our previous experience with dopexamine here in York; we cannot help the problem with randomization, the reader has to interpret the overall results with this particular problem in mind.
Again, in our discussion we defended the use of the POSSUM score: Dr Bayly argues that the fact that the actual mortality in our study is lower than that predicted by POSSUM demonstrates that the POSSUM score is not valid. Our previous experience would suggest otherwise. These patients were higher than average risk for their operation type. Recently published audits of outcome from major elective surgery in the UK,4 5 would suggest that the mortality rates in our study were indeed low by national standards, and I counter-argue that this was a result of the intraoperative haemodynamic optimization strategy implemented in our study.
The dose of dopexamine was chosen, again, from our own experience in York as a dose that produces a clinically significant rise in cardiac index, as can be seen from Table 3 in our paper.1
Because of the problems highlighted, we would agree that the conclusions to be drawn from our results are not necessarily as clear as the pure statistical analysis would suggest, and, as ever, further investigation will inevitably be required.
R. J. T. Wilson
York, UK
References
1 Stone MD, Wilson RJT, Cross J, Williams BT. Effect of adding dopexamine to intraoperative volume expansion in patients undergoing major elective abdominal surgery. Br J Anaesth 2003; 91: 61924
2 Mackenzie SJ. Editorial. Should perioperative management target oxygen delivery? Br J Anaesth 2003; 91: 6158
3 Wilson J, Woods I, Fawcett J, et al. Reducing the risk of major elective surgery: randomised controlled trial of preoperative optimisation of oxygen delivery. BMJ 1999; 318: 1099103
4 Tekkis PP, Poloniecki JD, Thompson MR, Stamatakis JD. Operative mortality in colorectal cancer: prospective national study. BMJ 2003; 327: 1196201
5 McCulloch P, Ward J, Tekkis PP. Mortality and morbidity in gastro-oesophageal cancer surgery: initial results of ASCOT multicentre prospective cohort study. BMJ 2003; 327: 11927