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Rapid Responses: Rapid Responses published:
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Penicillin is the Treatment of Choice in Most Respiratory Infections.
- Friedrich Flachsbart (23 August 2004)
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When is a randomised trial a randomised trial?
- Stephen J Conaty (25 August 2004)
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The experimental unit is wrong
- J Martin Bland (27 August 2004)
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Re: Penicillin is the Treatment of Choice in Most Respiratory Infections.
- Ineke Welschen, Marijke M Kuyvenhoven, Arno W Hoes, Theo JM Verheij (11 September 2004)
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Reply to Dr Stephen J Conaty. When is a randomised trial a randomised trial?
- Ineke Welschen, Marijke M kuyvenhoven, Arno W Hoes, Theo JM Verheij (11 September 2004)
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Re: The experimental unit is wrong
- Ineke Welschen, Marijke M Kuyvenhoven, Arno W Hoes, Theo JM Verheij (14 September 2004)
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Friedrich Flachsbart, General Medicine Praxis 37085 Göttingen
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Dear Sir, the authors Kuyvenhoven and Verheij cite their own work (1). Here they point to the real problem: "The international trend of a decline in the use of narrow-spectrum and older penicillins and prescribing more broad-spectrum and new chemotherapeutics." And they ask for the right solution: "More emphasis on implementation of guidelines aimed at prescribing narrower spectrum and older penicillins in respiratory tract infections and especially lower respiratory tract infections seems to be needed.." Penicillin is the treatment of choice in most cases. Nothing else. Sincerily Yours Friedrich Flachsbart 1. MM. Kuyvenhoven, FAM van Balen, TJM Verheij: Outpatient antibiotic prescriptions from 1992-2001 in The Netherlands. Journal of Antimicrobial Chemotherapy 2003;52:675-678 Competing interests: None declared |
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Stephen J Conaty, Consultant in Public Health Islington Primary Care Trust, 110 Hampstaed Rd, London NW1 2LJ
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The aphorism among epidemiologists "never leave randomisation to chance" seems to have been taken seriously by Welshen and colleagues in their study of an educational intervention to reduce antibiotic prescribing in GP peer groups. (1) The randomisation process in their study seems to have been reduced to a single coin toss after they had divided 12 GP peer groups into roughly equal camps with respect to three factors - rurality, prescribing and number of GPs. They seem to have done a good allocation job judging by the baseline characteristics in the two groups. However, none of the balance between groups is attributable to randomisation. The objective of randomisation is to achieve a balance between two comparison groups at baseline with respect to factors we know are important (i.e. can influence the outcome) and (this is the crunch) factors that we don't know about but are still important. Unfortunately in this trial we can't be confident that this high standard of balance was achieved because allocation to intervention or control group was not random. The only random element in this study (coin toss) simply decided which of these potentially imbalanced groups got the intervention. Randomisation is no guarantee of perfect balance and this is why epidemiologists and statisticians try to insure against gross imbalance by various means (2) – hence the aphorism above. The BMJ should consider carefully which trials deserve the label "randomised controlled trial" because this is often interpreted as a mark of quality. I think this trial is better labelled a "controlled trial" - no shame there. 1. Welschen I, Kuyvenhoven MM, Hoes AW, Verheij TJM. Effectiveness of a multiple intervention to reduce antibiotic prescribing for respiratory tract symptoms in primary care: randomised controlled trial. BMJ 2004;329:431-3. 2. Altman D, Bland M. Statics notes: Treatment allocation in controlled trials: why randomise? BMJ 1999;318:1209. Competing interests: None declared |
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J Martin Bland, Professor of Helath Statistics University of York, YO10 5DD, UK,
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Conaty is right to criticise the design of this trial. It is a randomised trial, in that something is allocated to treatment at random. In such a trial, the thing which is allocated is known as the experimental unit and is the smallest thing which can have a different treatment from another, similar unit. Here this is not the GP or the peer review group but the combined group of six peer review groups. In a cluster randomised trial, the cluster forms the experimental unit and should be used as the unit of analysis or have the variation between clusters included in some equivalent way. Welschen and colleagues have done this, taking the peer review group as the cluster. But it is not, it is the super-cluster of six peer review groups that is the experimental unit and should be the unit of analysis. Hence they have only two observations, one in each treatment group, and cannot estimate the variation between them. Hence then cannot tell whether the difference between the treatment groups is greater than would be likely to arise given the variation between experimental units. Hence they cannot analyse this as a randomised trial. The authors could have attempted to balance their two groups of six peer review groups by minimisation. They could then have analysed the trial as a cluster randomised trial in the usual way. Competing interests: None declared |
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Ineke Welschen, researcher Utrecht, the Netherlands, Marijke M Kuyvenhoven, Arno W Hoes, Theo JM Verheij
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Dear Sir, Indeed the decline in use of narrow spectrum and older penicillins and the increase in prescribing more broad-spectrum and new chemotherapeutics is one of the major problems in modern health care relating to the growing problem of antimicrobial resistance of bacterial agensts. However, even in the Netherlands about half of the antibiotic prescriptions for respiratory tract infections are unnecessary and inappropriate. This has not only been suggested by de Melker (1), but has recently been shown by our own research group (2). So, we believe the reached reduction is suboptimal; a higher reduction is possible as well as improving the choice of antibiotics is needed. Sincerely Yours, Ineke Welschen Marijke M Kuyvenhoven Arno W Hoes Theo JM Verheij 1. De Melker RA. Effectiviteit van antibiotica bij veel voorkomende luchtweginfecties in de huisartspraktijk. Ned Tijdschr Geneeskd 1998;142: 452-6. 2. Akkerman AE, Kuyvenhoven MM, van der Wouden JC, Verheij TJM. Het voorschrijven van antibiotica door de huisarts bij luchtweginfecties, astma en COPD. Submitted 2004 Competing interests: None declared |
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Ineke Welschen, researcher Utrecht, The Netherlands, Marijke M kuyvenhoven, Arno W Hoes, Theo JM Verheij
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Dear Sirs, Implementing guidelines requires comprehensive approaches at different levels (GPs, practices and peer review groups). Thus intervention studies on the effectiveness of quality improvement programmes should be pragmatic and embedded in existing structures. Conaty states that the used randomisation scheme is not a randomisation in the sense of random allocation of peer review groups aiming to make two groups comparable regarding known and unknown potential confounders. We agree that our scheme is not randomisation in that classical sense. However randomisation of peer review groups without matching or clustering was not an attractive option because randomisation of the - only - twelve peer review groups almost certainly would lead to differences in the important prognostic factors (or if you wish ‘confounders’) between the intervention and control group. That is why we developed a method to ensure comparability of the three major potential confounders (a) degree of urbanisation (rural/urban), (b) group size (above / below median) and (c) volume of antibiotic prescriptions (above / below median) between the two groups. Otherwise sample sizes would not have been feasible. This ended up with two comparable groups of GP peer review groups, which were randomly allocated to the experimental and control group. The solution chosen after consultation of several statisticians and epidemiologists was perhaps unusual, but did in their and our firm opinion not bias the results and Conaty seems to agree with that. Consequently we defined to present the trial as a randomised controlled trial; using the concept of “controlled trial” would neglect the random allocation of the combined groups of GP peer review groups. Bland critizes the statistical analysis at the level op GPs, while allocation and randomisation was carried out at the level of combined groups of GP peer review groups. The randomisaton scheme we applied to obtain comparable groups does not imply that the unit of statistical analysis had to be the combined groups of GP peer review groups; even if this was statistically possible it would result in clinically irrelevant results, since the intervention was directed to individual GPs within peer review groups and was aimed to change GP behaviour. So we calculated effectiveness at GP level “controlling” for practice and GP peer group level. Importantly, taking these two “clustering” factors into account did not clearly influence the results. Sincerely Yours, Ineke Welschen Marijke M Kuyvenhoven Arno W Hoes Theo JM Verheij Competing interests: None declared |
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Ineke Welschen, researcher utrecht the netherlands, Marijke M Kuyvenhoven, Arno W Hoes, Theo JM Verheij
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Dear Sir, Implementing guidelines requires comprehensive approaches at different levels (GPs, practices and peer review groups). Thus intervention studies on the effectiveness of quality improvement programmes should be pragmatic and embedded in existing structures. Conaty states that the used randomisation scheme is not a randomisation in the sense of random allocation of peer review groups aiming to make two groups comparable regarding known and unknown potential confounders. We agree that our scheme is not randomisation in that classical sense. However randomisation of peer review groups without matching or clustering was not an attractive option because randomisation of the - only - twelve peer review groups almost certainly would lead to differences in the important prognostic factors (or if you wish ‘confounders’) between the intervention and control group. That is why we developed a method to ensure comparability of the three major potential confounders (a) degree of urbanisation (rural/urban), (b) group size (above / below median) and (c) volume of antibiotic prescriptions (above / below median) between the two groups. Otherwise sample sizes would not have been feasible. This ended up with two comparable groups of GP peer review groups, which were randomly allocated to the experimental and control group. The solution chosen after consultation of several statisticians and epidemiologists was perhaps unusual, but did in their and our firm opinion not bias the results and Conaty seems to agree with that. Consequently we defined to present the trial as a randomised controlled trial; using the concept of “controlled trial” would neglect the random allocation of the combined groups of GP peer review groups. Bland critizes the statistical analysis at the level op GPs, while allocation and randomisation was carried out at the level of combined groups of GP peer review groups. The randomisaton scheme we applied to obtain comparable groups does not imply that the unit of statistical analysis had to be the combined groups of GP peer review groups; even if this was statistically possible it would result in clinically irrelevant results, since the intervention was directed to individual GPs within peer review groups and was aimed to change GP behaviour. So we calculated effectiveness at GP level “controlling” for practice and GP peer group level. Importantly, taking these two “clustering” factors into account did not clearly influence the results. Sincerely Yours, Ineke Welschen
Competing interests: None declared |
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