Statistics

To the Editor: We are writing to add our wholehearted support to the plea made by Carapetis et al1 for a simplified ethical approval process for multicentre studies. We are conducting two national case-controlled studies of cancer in Australia, funded by grants from the National Institutes of Health and the Department of Defense in the United States, as well as the National Health and Medical Research Council (NHMRC). Our ability to achieve full population coverage was a major competitive advantage in terms of securing international funding. However, to realise this objective, we have spent more than a year obtaining ethics approval from the myriad institutions controlling access to patients and the public. We have been required to make more than 60 separate ethics applications, lodging about 550 copies of the proposal (a total of 40 000 sheets) at a cost of more than $7000 for paper and printing alone. When labour is included the cost of the initial submissions escalates to $16 000 (excluding substantial investigator time). Other costs include the extraordinary requirement of one ethics committee in Victoria that an investigator from Queensland personally attend a 10-minute interview at which no substantive issues were raised. The ethical benefit of this investment must be questioned when the majority of changes required by committees have dealt with minor issues such as grammatical style that have little to do with patient protection. Inevitably, such directives are inconsistent across institutions. It is thus impossible to comply with all requests while maintaining a standard set of study documents. These problems are accentuated for the increasing number of Australian researchers relying on overseas funding. For example, regulatory authorities in the United States insist that all ethics committees reviewing US-funded projects involving humans must have US federal approval to do so. In our experience, few Australian hospital ethics committees have this approval. Therefore, in addition to fulfilling standard institutional ethics requirements, we have also had to help several committees go through the lengthy process of securing US accreditation simply to approve our study! For all the above reasons, we strongly believe that Australian researchers and patients would be best served by a single national ethics committee for large multicentre studies. This would also reduce the enormous burden currently placed on the individual committees. In the meantime, we thank Breen and Hacker2 for their reminder to institutional ethics committees that the NHMRC national statement "empowers ethics committees to minimise unnecessary duplication".

David C Whiteman · Penelope M Webb · David M Purdie · Adèle C Green

Self-experimentation in Australia is alive and well Many advances in modern medicine owe a great deal to human experimentation. Indeed, much of biomedical research is irrelevant to mainstream medicine unless its clinical utility is established through human experimentation, for, as observed by the English essayist Alexander Pope, "the proper study of mankind is man."1 Today the circumstances and conduct of human experimentation are painstakingly policed by ethics committees, but even such strict surveillance cannot guarantee safety: "because experiments with humans are voyages into the unknown, an element of risk is always involved; the potential for death, injury, or illness can be reduced, but it can not be eliminated."2 It is this very uncertainty that presents a dilemma for researchers. Sir George Pickering, past Regius Professor of Medicine at Oxford, delineated this quandary: "The experimenter has one golden rule to guide him . . . Is he prepared to submit himself to the procedure? If he is, and if the experiment is actually carried out on him, then it is probably justifiable. If he is not, then [it] should not be done."2 In short, the researcher should be the guinea pig. Risk-laden stories of researchers being guinea pigs abound in medicine's heritage. They include that of John Hunter, the 18th-century English anatomist and surgeon, who allegedly inoculated himself with venereal pus. The symptoms of gonorrhoea and primary syphilis were soon apparent and during the last 15 years of his life he was plagued by a legacy of angina pectoris presumably due to tertiary syphilis.2,3 Other celebrated accounts include that of Werner Forssmann, who, in the 1920s, catheterised his heart with ureteric tubes. This risk-laden technique lay fallow until the 1940s, when Cournand and Richards in the United States refined and employed it in ground-breaking work in cardiorespiratory physiology. In 1956, all three were awarded the Nobel Prize in Medicine or Physiology.2 In the 1950s the enthusiasm for self-experimentation within the Department of Internal Medicine at Washington University, St Louis, earned it the name the "Kamikaze School of Medicine".2 Bill Harrington, a young researcher, courted death from cerebral haemorrhage with profound thrombocytopenia after being infused with plasma from a patient with idiopathic thrombocytopenic purpura (ITP).2 A fellow researcher, Tom Brittingham III, repeatedly injected himself with leukaemic white cells in an attempt to produce white-cell antibodies. He almost killed himself when he had an anaphylactoid reaction accompanied by profound hypotension and severe pulmonary oedema after being infused with plasma from a patient with aplastic anaemia.2 Nonetheless, these unsettling self-experiments established the immune basis of ITP and white-cell-associated transfusion reactions. Harrington's work inspired Jan Dausset of Paris to pursue research into the immunology of ITP and white cells, which culminated in his being awarded the 1980 Nobel Prize for demonstrating human leukocyte antigen (HLA; the transplantation antigen) in white cells.2 Australian researchers have also succumbed to the human guinea pig syndrome. In 1951, as the first wave of myxomatosis raced along the Murray River, its arrival in Mildura coincided with an outbreak of Murray Valley encephalitis in the surrounding district. The public was gripped by fear that the myxoma virus was responsible for the outbreak of encephalitis. This fear reached such heights that the chairman of Mildura Base Hospital challenged R G Casey, the Minister responsible for the Commonwealth Scientific and Industrial Research Organisation (CSIRO), and Sir Frank Macfarlane Burnet, Director of the Walter and Eliza Hall Institute (WEHI), to test the harmlessness of the myxoma virus on themselves! Spurred on by intense media pressure, Macfarlane Burnet, Frank Fenner (Professor of Microbiology at the John Curtin School of Medicine, but working at WEHI) and Ian Clunies Ross (Director of the CSIRO) inoculated themselves with enough myxoma virus to kill 100–1000 rabbits. All three suffered no harm, and in true political style this fact was made public by Casey through an announcement in Federal Parliament.4 The culture of the Kamikaze School of Medicine was further manifest when Australian clinical researchers performed radiolabelled platelet studies on themselves,5 or underwent unpleasant bone marrow aspirations to procure marrow cells for drug studies.6,7 Finally, the experiments of Barry Marshall, who ingested Helicobacter pylori,8 are now legend in medicine. His self-experiments eventually turned prevailing concepts of peptic ulcer causation and treatment on their head. Now, in the new millennium, the report in this issue of the Journal by Landmann and Prociv attests that self-experimentation in Australia is alive and well. In a series of self-experiments these investigators have shown that dog hookworm (Ancylostoma caninum) infection causing symptomatic eosinophilic enteritis is more likely to enter the body orally than percutaneously.9 What drives researchers to be their own guinea pigs? Lawrence Altman, in his delightful book Who goes first? The story of self-experimentation in medicine, proposes a number of motivating factors.2 These include reliability (researchers being more likely to adhere compulsively to the research protocol), dependability (for observations and detecting problems with design), a spirit of adventure, first-hand experience, self-protection, convenience (avoiding the frustrations of recruiting and being involved in the nuances of informed consent) and experience (when the experiments involve risk, the experience of the researcher is important and many will risk exposing themselves rather than others). However, self-experiments are subject to criticism.2 Potential problems include loss of objectivity, cumulative exposure to risks and comorbidities in the self-researcher (including self-experimentation suicide), but particularly the inherent limitations of a research design focusing on a single subject.10 Despite all this, researchers who enlist as guinea pigs will continue to grace medical research. Modern research is increasingly complex, with sophisticated designs and statistics, bewildering technology and the added burden of the close monitoring of projects by ethics committees. This impersonal and mechanistic culture is far removed from the humanistic and romantic spirit of adventure embodied in altruistic self-experimentation. As long as human research is informed by the premise that "because we were venturing into the unknown . . . a man is entitled to risk his own life. He is not entitled to risk somebody else's",2 researchers as guinea pigs will always be with us.

Martin B Van Der Weyden MD, FRACP, FRCPA

A dream becoming a reality The Cochrane Library is now available free to all Australians who have Internet access. At the 3rd Annual Meeting for Australasian Contributors to the Cochrane Collaboration, held in Melbourne in October this year, the Federal Minister for Health and Ageing announced this important milestone — universal access to high-quality health information. Just as ready access to "clean" drinking water has come to be seen as a public health milestone of the 19th century, so, in the future, ready access to "clean" health information might well be dubbed as a major public health achievement of this century. The United Kingdom and Ireland, as well as several other countries in Europe, also have free access and the Library is also available free to developing countries. Such access will have a direct impact on satisfying clinicians' daily information needs, and an indirect impact on their practices through the information accessed by patients, consumer organisations, policymakers, and others. So where will this lead us? To understand some of the implications requires an understanding of both the history and the future of the Cochrane Collaboration.1 In 1979, a challenge came from the UK epidemiologist Archie Cochrane, who stated: "It is surely a great criticism of our profession that we have not organised a critical summary, by speciality or subspeciality, adapted periodically, of all relevant randomised controlled trials."2 Meeting Cochrane's challenge required two important steps: (i) assembling all controlled trials in one database, and (ii) completing and maintaining systematic reviews of these trials. The first step corresponds to the Cochrane Central Register of Controlled Trials, which now includes over 350 000 trials, and the second to the Cochrane Database of Systematic Reviews, which currently contains 1456 complete Cochrane reviews, and the protocols for 1101 planned reviews. How did the Cochrane Library come to be? In Cochrane's 1979 article1 he challenged the medical profession in general, but singled out obstetrics as the specialty most in need of an evidence base from controlled trials. When Iain Chalmers (who had worked in obstetrics) became Director of the UK National Perinatal Epidemiology Unit in 1978, he initiated a classified bibliography of randomised trials of interventions in pregnancy, childbirth and early infancy, using both electronic searches and manual searches of over 60 journals. This bibliography provided the raw material for an international collaboration to prepare systematic reviews, which were eventually published in 1989 in a seminal, two-volume, 1500-page book entitled Effective care in pregnancy and childbirth.3 The book concluded with a chapter summarising which interventions (of the 283 assessed) were supported by reasonably strong research evidence (100 were deemed effective, 36 promising, 86 of unknown benefit and 61 so unlikely to be useful that they should be abandoned). Importantly, not only was a paperback summary prepared for women published concurrently, but also a six-monthly electronic update of the systematic reviews — the Oxford Database of Perinatal Trials. This "pilot" project was well received. In 1992, the UK National Health Service provided crucial support for Chalmers to work with others to extend the process to other areas of healthcare. Recognising that the work could not be done by a single group or country, the international Cochrane Collaboration was founded in 1993 at the first Cochrane Colloquium, held in Oxford. Two years later the Cochrane Database of Systematic Reviews was launched, and the late Chris Silagy, inaugural Director of the Australasian Cochrane Centre, became the first elected Chair of the Steering Group, guiding the growth of reviews prepared by members of 49 Collaborative Review Groups, which, collectively, are responsible for covering most health problems. At the 1995 Cochrane Colloquium, David Sackett described the Cochrane Collaboration as a plane that took off while it was still being built. In 2002, the Collaboration is flying at a respectable altitude. But what still needs to be done for Cochrane's dream to become a reality? One sobering fact is that less than 10% of more than 350 000 published controlled trials have been synthesised within Cochrane reviews. To complete the journey will require three things: Review efforts will need to be sustained and extended by appropriate support and training in systematic reviewing. The science of research synthesis will need to develop an academic capacity and infrastructure equivalent to those of other fields of specialised medical endeavour. To maximise clinical relevance and uptake, the Library interface and reviews have to become more attuned to the needs of users and the users need to be more sophisticated in applying evidence. Reviewers will need to have access to all trials, not just those published in electronically indexed journals. Registration of all trials at inception is necessary, and is becoming a reality (see the meta-register at www.controlled-trials.com). Finally, we need to recognise that the Cochrane Library synthesises only intervention studies. At the 1996 Cochrane Colloquium, Hilda Bastian, chair of the Cochrane Consumer Network, suggested "people often ask if we can afford to extend the Collaboration beyond the RCT; we also need to consider whether we can afford not to do so". We will also need more systematic use of non-randomised study data on harms or treatments, and equivalent collaborations for systematic reviews of the accuracy of diagnostic tests, the natural history and prognosis of disease, and other types of clinical questions (see, for example, a description of Bayes Library of Diagnostic Studies and Reviews: <www.bice.ch/engl/content_e/bayes_library.htm>). In brief, although the announcement of free access to the Cochrane Library is an important and welcome milestone, much work remains to be done to make best use of the presently available results of clinical research relevant to the wellbeing of users of health services. Sceptics might ask what evidence there is that ready access to such databases will make a difference. Free access might be seen as an ethical obligation — in return for the public's participation and direct or indirect funding of research. However, adequate evaluation is also essential to both assess the impact and to guide improvements. The National Institute of Clinical Studies (<www.nicsl.com.au/>), which brokered the free Cochrane Library access, will also undertake an evaluation that will include process measures, such as who is accessing what, and a more detailed study of the difficulties and needs of end-users. However, we should recognise that information access is a necessary, but not sufficient, condition to bridge the gap between research and practice. It may be far from enough. Hence, more detailed evaluation might be planned to explore factors such as the impact of clinicians' skills in using evidence, attitudes to applying evidence, structural barriers to using proven interventions, and problems in matching evidence to individual patients' needs that limit any potential benefits of free access.

Paul P Glasziou PhD, FRACGP

Randomisation is the process of assigning clinical trial participants to treatment groups. Randomisation gives each participant a known (usually equal) chance of being assigned to any of the groups. Successful randomisation requires that group assignment cannot be predicted in advance. Why randomise?If, at the end of a clinical trial, a difference in outcomes occurs between two treatment groups (say, intervention and control) possible explanations for this difference would include: the intervention exhibits a real effect; the outcome difference is solely due to chance; or there is a systematic difference (or bias) between the groups due to factors other than the intervention. Randomisation aims to obviate the third possibility. Allocation of participants to specific treatment groups in a random fashion ensures that each group is, on average, as alike as possible to the other group(s). The process of randomisation aims to ensure similar levels of all risk factors in each group; not only known, but also unknown, characteristics are rendered comparable, resulting in similar numbers or levels of outcomes in each group, except for either the play of chance or a real effect of the intervention(s). Statistical analyses of clinical trials assume that randomisation was used and was "successful". The analytic tests used give the likelihood of chance explaining a difference of at least the magnitude observed. If this likelihood is small, we conclude that the observed difference was due to a real effect of the intervention. Successful randomisation allows for valid statistical interpretation of "raw" results (ie, estimates that are unadjusted for other patient characteristics). However, successful randomisation does not guarantee perfect balance in risk factors between groups (due to the play of chance), so adjusted analyses can also help in further interpretation of outcome results. In a clinical trial report, it is important to document that random allocation of treatment assignment was successfully achieved. The CONSORT statement1 suggests that the sequence generation, allocation concealment and implementation be reported (Box 1). Sequence generationSimple randomisationSimple randomisation is the most basic method of random treatment assignment. This can be thought of as tossing a coin for each trial participant, A being allocated with "heads", B with "tails". However, it is not usually performed using a real coin-toss, as issues of concealment, validation and reproducibility arise (see below). Simple randomisation is usually achieved using a sequence of random numbers from a statistical textbook, or a computer-generated sequence. Permuted block randomisationIn a large trial (at least 1000 subjects), simple randomisation should give a balance in number of patients allocated to each of the groups in the trial, but for a "small" study the numbers allocated to each group may not be well balanced. In small trials, to maintain good balance, blocked randomisation may be used. "Blocks" having equal numbers of As and Bs (A = intervention and B = control, for example) are used, with the order of treatments within the block being randomly permuted (Box 2). A block of four has six different possible arrangements of two As and two Bs.2,3 A random number sequence is used to choose a particular block, which sets the allocation order for the first four subjects. Similarly, treatment group is allocated to the next four patients in the order specified by the next randomly selected block. The process is then repeated. Permuted block randomisation ensures treatment group numbers are evenly balanced at the end of each block. Stratified allocationStratified block randomisation can further restrict chance imbalances to ensure the treatment groups are as alike as possible for selected prognostic variables or other patient factors. A set of permuted blocks is generated for each combination of prognostic factors. For example, in a trial of chemotherapy for breast cancer, suitable stratification factors might be menopausal status and oestrogen-receptor status. A set of permuted blocks is generated for those women who are premenopausal and oestrogen-receptor negative, another set for those who are premenopausal and oestrogen-receptor positive, and so on. Stratification can add to the credibility of a trial, as it ensures treatment balance on these known prognostic factors, allowing easy interpretation of outcomes without adjustment. Dynamic (adaptive) random allocation methodsSimple and block randomisation methods are defined, and allocation sequences set up, before the start of the trial. In contrast, dynamic randomisation methods allocate patients to treatment group by checking the allocation of similar patients already randomised, and allocating the next treatment group "live" to best balance the treatment groups across all stratification variables. Minimisation3 is one such method, and can be implemented using a manual card system, but dynamic methods are best implemented on computer (Box 3). Inappropriate randomisation methodsMethods of allocation such as alternate allocation to treatment group, or methods based on patient characteristics such as date of birth, order of entry into the clinic or day of clinic attendance, are not reliably random. Such allocation sequences are predictable, and not easily concealed, thus reducing the guarantee that allocation has indeed been random, and that no potential subjects have been excluded by foreknowledge of the intervention. Concealment of the allocation processIt is very important that those responsible for recruiting people into a trial are unaware of the group to which a participant will be allocated, should that subject agree to be in the study. This avoids both conscious and unconscious selection of patients into the study. "Allocation concealment" is the term used to describe this process and underpins successful randomisation strategies.4,5 For multicentre clinical trials, central randomisation by telephone, interactive voice response system, fax or the Internet are ideal methods for allocation concealment. The clinician or data manager at the participating site assesses eligibility, gains consent, and makes the decision to enrol a patient, then calls the randomisation service to get the treatment allocation. Central randomisation also enables trial coordinators to monitor randomisation rates, and have a record of all allocated patients for potential follow-up. For single-centre clinical trials, it is usually possible to identify a staff member not involved with the trial who can keep the randomisation list or envelopes, preferably in a location away from the clinic or ward where patients are being assessed. For example, pharmacy staff may be able to undertake randomisation. They should be instructed to keep the list private, and to only reveal a treatment allocation after receiving information demonstrating that the patient is eligible and has consented to the trial. In situations where remote randomisation may not be feasible or desirable, a set of tamper-evident envelopes may be provided to each participating site. The envelopes should look identical, and each should have the trial identification and a sequential number on it. Inside is the treatment allocation and usually a trial identifier for the patient (eg, unique sequential number). After assessing eligibility and consent, as described above, the next envelope in sequence is opened. Care needs to be taken that the envelopes are opaque and well sealed, and that the sequence of opening the envelopes is monitored regularly. For example, the patient identifiers could be written on the envelope, and the contents of the envelope, along with the date and time of randomisation, transcribed to the randomisation form where eligibility assessment was recorded. Stratified randomisation is still possible using randomisation envelopes by having a set of envelopes for each combination of stratification factors. A screening log should be considered to help ensure that eligible patients were not missed, and were not excluded on the basis of study staff somehow knowing the next treatment allocation. Concealment through sequence generationAllocation concealment may be thwarted by an inappropriate choice of randomisation sequence generation. For example, a permuted block design with a fixed block size of four, in an unblinded study6 where treatment group is revealed at the time of randomisation, may make it easy to predict the next allocation once three patients have been randomised. For this reason, details of block size should not be revealed to investigators or other study staff. A varying block size can also be used (eg, blocks of size 4, 6 and 8 randomly arranged). Dynamic allocation methods provide a more secure method of allocation concealment. ImplementationThe trial statistician (or others not directly involved in recruiting patients to the trial) commonly generates the randomisation sequence. Methods that allow a permanent record of the sequence created are important to validate its randomness later if required (whereas a coin toss can be replaced without record). A clinical trial report should clarify who generated the sequence, the method used, and how concealment was achieved and monitored. There should be some demonstration that randomisation was successful. This is usually achieved by providing a table in a report comparing the major baseline demographic and prognostic characteristics of the two treatment groups. 1: CONSORT checklist of items to include when reporting a trial1 Section and topic Item no. Descriptor Methods Randomisation Sequence generation 8 Method used to generate the random allocation sequence, including details of any restriction (eg, blocking, stratification) Allocation concealment 9 Method used to implement the random allocation sequence (eg, numbered containers or central telephone), clarifying whether the sequence was concealed until interventions were assigned Implementation 10 Who generated the allocation sequence, who enrolled participants, and who assigned participants to their groups 2: The permuted block method of randomisation for a block size of four, with A and B being treatment groups (A = intervention and B = control, for example) A random number sequence is generated from a statistical textbook or computer. Each possible permuted block is assigned a number (1 to 6 in the above example). Using each number in the random number sequence in turn selects the next block, determining the next four participant allocations. Numbers in the random number sequence greater than the number of permuted block combinations (7, 8, 9 and 0 in the above example) are not used to select blocks. 3: Example of randomisation using the minimisation method in a trial of chemotherapy for breast cancer, with stratification factors of clinic site, oestrogen receptor status (ER+ or ER–) and menopausal status Status after 34 participants have been randomised to the trial Characteristic Treatment A Treatment B Site 1 7 8 Site 2 10 9 ER+ 5 6 ER– 12 11 Premenopausal 8 9 Postmenopausal 9 8 Total 17 17 The next participant (no. 35) is from Site 2, ER+, postmenopausal. Subtotals for treatment allocation to this profile of characteristics are 10 + 5 + 9 = 24 for Treatment A and 9 + 6 + 8 = 23 for Treatment B (note subjects are counted more than once). Participant no. 35 would therefore be allocated to Treatment B. When the tallies on A and B are equal within a profile, the next participant is randomly allocated. This process is equivalent to a permuted block size of two within the profile. 4: Checklist for choosing a randomisation strategy How many subjects and clinical sites are planned? Are 24-hour randomisation services required? How will randomisation be implemented: central, remote local, bedside? Who will generate the sequence and by which method: random number lists, computer? Is a stratified or simple randomisation needed? If stratified, how many strata and levels within each stratum are required? What balancing strategy should be chosen: simple, permuted blocks, minimisation? What measures will be taken to guarantee allocation concealment? Who is going to monitor successful implementation (the balance of treatment allocation, unblinding rates) during recruitment? Should a screening log of eligible subjects be collected to ensure patients are not excluded by foreknowledge of treatment allocation? Queensland Clinical Trials Centre, University of Queensland, Herston, QLD. Elaine M Beller, MAppStat, Director of Biostatistics. NHMRC Clinical Trials Centre, University of Sydney, Camperdown, NSW. Val Gebski, MStat, Principal Research Fellow; Anthony C Keech, FRACP, MScEpid, Deputy Director. Correspondence: Associate Professor Anthony C Keech, NHMRC Clinical Trials Centre, University of Sydney, Locked Bag 77, Camperdown, NSW 1450. enquiryATctc.usyd.edu.au AntiSpam note: To avoid spam, authors' email addresses are written with AT in place of the usual symbol, and we have removed "mail to" links. Replace AT with the correct symbol to get a valid address.

Elaine M Beller MAppStat · Val Gebski MStat · Anthony C Keech FRACP, MScEpid

To the Editor: The Victorian Health Records Act 2001 became operational on 1 July 2002. This legislation provides important protection for the individual against misuse of health information through the establishment of Health Privacy Principles. We support the spirit of this legislation, but would like to draw attention to its potential effects on multicentre research and disease surveillance. We recently began a study to estimate the burden of invasive group A streptococcal disease in Victoria. The study involves identification of patients through laboratory notifications, followed by collection of clinical data — a strategy similar to surveillance of notifiable diseases. The study is funded by the National Health and Medical Research Council. We have sought institutional ethics committee approval, and are obtaining individual informed consent from patients. Despite approval from the Human Research Ethics Committee of the Victorian Department of Human Services, concerns arising from the new privacy legislation led most Victorian healthcare institutions to also require approval by their own ethics committees. We have now applied to over 30 separate committees, and the process is not yet complete. This has been an enormous drain on resources, has necessitated our establishing complex administrative procedures, and delayed commencement of the project. Moreover, many committees have required that we pay an application fee of several hundred dollars. Some have been uncertain about the implications of the new legislation for our project, and have requested clarification from the Victorian Health Services Commissioner. Despite these processes, some clinicians we have contacted are unwilling to allow their patients to be approached for fear of breaching privacy legislation. Our protocol is not controversial, and no substantive issues have been raised by any of the ethics committees. While ethical clearance is crucial to the success of the project, we were unprepared for the amount of work, confusion and expense involved. It is possible that these difficulties could discourage other researchers from conducting similar studies in Victoria. Similar concerns have been raised in the United Kingdom since the introduction of new privacy laws.1 The Victorian legislation allows for research and surveillance activities using identifying data if they are in the public interest, or if it is impracticable to seek individual consent. However, the legislation does not provide guidelines on what constitutes public interest or when consent is impracticable. The extent to which this legislation affects multicentre research or surveillance projects needs to be clarified, and a more simplified ethical approval process for surveillance activities identified.

Jonathan R Carapetis · Jonathon W Passmore · Kerry Ann O'Grady

Comment: It is unfortunate that a valuable research project has apparently been made more difficult or delayed by the combination of complex new privacy law and longer-standing inefficiencies in the ethical review of multicentre research proposals. Both are issues with which the Australian Health Ethics Committee (AHEC) is grappling at present. Multicentre research was identified as a significant issue in the review that led to the revised 1999 National Statement on Ethical Conduct in Research Involving Humans.1 The Statement makes it clear that researchers have a role in negotiating with human research ethics committees and institutions to seek agreement that the ethical and scientific assessment of one committee or institution will be accepted by other sites. The National Statement equally empowers ethics committees to minimise unnecessary duplication. Ethics committees have been very slow to grasp the opportunities offered by the 1999 National Statement for reasons that may include the past practice of insisting that each committee make its own assessment. Initiatives are now in train in New South Wales, Victoria, Western Australia and Queensland to develop different forms of centralised assessment, but the benefits may take time to be realised. AHEC, through its bulletins and workshops for ethics committee members, has repeatedly reminded committees how to simplify multicentre review, but traditional practices appear to have obstructed this message. This letter is yet another opportunity to remind ethics committees and institutions that the National Statement permits and encourages them to exercise initiative, judgement and common sense in facilitating effective and timely review of multicentre research. With regard to the difficulties associated with the new privacy regimes being put in place by a combination of federal and State laws, AHEC anticipated some introductory problems in relation to human research. It is understandable that ethics committees and researchers will take time to adjust some of their established practices to comply with the law and associated guidelines. During the period of adjustment, some flexibility needs to be exercised by all parties. AHEC conducted a series of workshops in all capital cities earlier this year to assist researchers and ethics committees in this phase. An explanatory guide to the use of privacy law and the associated guidelines from the National Health and Medical Research Council was used at these workshops and will be made more widely available shortly. Finally, the federal legislation will be the subject of a systematic review after two years. Unintended consequences of the law should be addressed at that time. AHEC understands that, in Victoria, the Health Services Commissioner, whose office has responsibilty for supervising the application of the health privacy law, is in the process of producing a practical guide for Victorian healthcare researchers.

Kerry J Breen · Sandra M Hacker

Comment: As I understand Carapetis et al's study, the researchers determine who has a group A streptococcal infection from the laboratory that performs the test (as this infection is not a notifiable disease,1 there is no central source of information). The laboratory may be independent or in a public or private hospital, and may be situated anywhere in Victoria. The laboratory tells them who requested the test and the patient's name and infection status. The researchers then seek assistance from the hospital or doctor requesting the test in obtaining "individual informed consent" from the patient to release clinical information to the researchers. Each institution has required that its own human research ethics committee approve the project, as well as the Department of Human Services (DHS) Ethics Committee, before the laboratory releases information. This accords with the law, but the additional bureaucracy and costs involved will deter much important public health research. The law: In Victoria, public and private hospitals and their employees have a statutory duty of confidentiality under section 141 of the Health Services Act 1988 (Vic). There is an exception when the patient consents (s 141(3)(a)), but, in Carapetis et al's study, patients cannot be approached until the laboratory gives identifying information. Information may be divulged for medical research without patient consent if an ethics committee "established under the by-laws of the agency" has approved "the use to which the information will be put and the research methodology" (s 141(3)(g)). The giving of information must also accord with Health Privacy Principle (HPP) 2.2(g) in the Health Records Act 2001 (Vic): it must be necessary and "in the public interest"; it is impracticable to seek consent; identifying information is needed; identifying information will not be published; and it must conform with the Guidelines of the Health Services Commissioner.2 The federal Privacy Act 1988 (Cwlth) contains similar provisions.3 Options for change: The Health Services Commissioner has power to issue guidelines varying the subparagraphs of HPP 2, and even to lessen the level of privacy protection, if it is in the public interest to do so.4 However, guidelines cannot override the requirement in the Health Services Act that projects must be approved by the ethics committee "established under the by-laws of [each] agency". There are four options for change: The Health Services Act could be amended so that approval of one human research ethics committee is sufficient. The Secretary of the DHS could prescribe more diseases as notifiable,1 so that information is available centrally, and access could be authorised by the DHS Ethics Committee. The Secretary could request information from pathology laboratories for public health research and supply that to the researchers (laboratories would be protected under section 137 of the Health Act 1958 [Vic]). Institutions could amend their by-laws — or ethics committees could adopt a policy — that the institution will follow the approval of the DHS Ethics Committee in public health research.5 The last seems the simplest option, but historically this approach has not been favoured in multicentre trials in Australia.

Loane LC Skene

Trial evidence best informs real-world medicine when it is relevant to the clinical problem Controlled clinical trials provide the most reliable evidence of whether treatments are effective, particularly when the effects of treatment are moderate. Without such trials, ineffective treatments or, even worse, harmful interventions may be accepted in medical practice. Yet medical practice is often not based on clinical trial evidence, because the evidence is considered not relevant or does not exist. Real-world medicine must not only consider the effectiveness of specific treatments, but must do so in the context of patients who have multiple problems and who are often already receiving many different treatments in a setting different from that tested in the trial.1 Throughout the history of medicine, many treatments have been considered effective until well-controlled trials demonstrated otherwise.2 Some recent treatments based on observational data that have been discredited by randomised controlled trials include hormone replacement therapy to prevent coronary heart disease events,3 vitamin supplements to prevent lung cancer4 or cardiovascular disease events,5 and arthroscopic surgery for osteoarthritis of the knee.6 Although data from observational studies may be of value,7 these data may sometimes suggest a harmful outcome for treatments that are known, from controlled trials, to be effective, such as blood pressure treatment.7 Applying trial results to individual patientsAlthough clinical trial evidence for the introduction and use of new drugs is widely accepted, the "real-world" uptake is often erratic. For patients with coronary heart disease, the merits of statins, angiotensin-converting enzyme (ACE) inhibitors, β-blockers and aspirin are well recognised from clinical trial evidence, yet these treatments are still significantly underused.8 The gap between evidence and practice is even wider in other areas. Evidence is an essential part of good medical practice, but it is not the only information needed for clinical decision-making. Real-world medicine may ignore clinical trial evidence if it does not seem relevant to the clinical problem at hand or if the benefit is uncertain. A drug that shrinks a cancer is not necessarily useful unless it also improves the patient's quality of life or prolongs survival. A treatment that lowers blood pressure or cholesterol has value only if these outcomes are translated into meaningfully fewer cardiovascular events, without a penalty of increased adverse effects. Hence, evidence from trials is most applicable in practice when the design and the outcomes chosen are directly relevant to real patients, the trials are undertaken against a background of standard medical care, patients in trials are broadly representative of patients in the real world, and evidence from trials is integrated with individual patient characteristics for meaningful risk–benefit assessment. Absolute differences in risk (or numbers needed to treat) are recognised as most relevant to decision making; yet clinical trial results are often reported as changes in relative risk. For example, recent clinical trial results of breast cancer risk in women taking hormone replacement therapy appeared exaggerated if the increased risks were considered in relative rather than absolute terms. Treatment resulted in a 26% relative increase in breast cancer, which equated to an absolute increase of just 0.08% per year.3 Nevertheless, the relative treatment effect is of value if applied appropriately (by combining it with the individual's baseline risk), providing a better guide to the absolute effect of treatment in specific patient groups.1 ParticipationDespite the need for high-quality clinical trials, few patients participate in them, even in areas where trials are common. For example, less than 5% of eligible patients participate in most cancer trials9 and less than 10% in many cardiovascular trials.10 Low participation rates raise concerns that the results from trials apply only to select groups of patients. Scant participation is not necessarily a problem if patients are representative, but patients in trials are often narrowly selected because of the eligibility criteria, the setting, or the patients agreeing to participate. Strategies such as public access to ongoing trials through registers and more pragmatic trial designs are needed to maximise participation and ensure treatments are assessed in a variety of settings. The need for wider use of clinical trialsWhenever a new drug treatment is discovered that has the potential to help many patients, prevailing systems support well-controlled trials addressing effectiveness and safety. Systems to assess new technologies or interventions other than drugs are equally important, yet more challenging and much less developed. Also lacking are sufficient trials of new devices, health service management decisions, and trials in community or Third World settings. It has been suggested that clinical trials are too expensive, and funding outside the pharmaceutical industry is limited. A randomised clinical trial, evaluating a moderate treatment effect on important clinical outcomes, may cost from $1 million to more than $50 million. However, this cost needs to be put in the context of healthcare generally (more than $50 billion in Australia each year11) and the cost of not undertaking trials before deciding which treatments to support. The Australian government has recognised the importance of basing funding decisions for new health technologies (through the Pharmaceutical Benefits Advisory Committee and the Medicare Services Advisory Committee) on the best evidence of the effectiveness, safety and cost-effectiveness of each treatment. But funding more research on the cost-effectiveness of new technologies is also warranted. Specific clinical trials in this context may be much more cost-effective than using funds to introduce therapies on the basis of less reliable evidence.12 Consequently, a more proactive funding strategy for trials should be considered, extending the model proposed by Glasziou: 13 up to 1% of the national healthcare budget could be used to test new and existing health technologies for which there is inadequate evidence, but potentially large benefits or cost savings.14 One approach to monitor and implement some of these strategies is through the use of a comprehensive national trials register to aid the planning of new trials, ensure all trials are identified when evaluating trial evidence, and maximise participation of patients and doctors in ongoing trials.15 Many clinical trials already play a central role in everyday clinical practice. However, if we seriously address each of the above issues, health outcomes could be further improved through clinical trials assessing new health technologies and existing treatments in the real world of modern medicine. It is time for us to look at how to make this more of a reality.

R John Simes

In planning clinical trials, it is common to find that the calculated sample size1 (Item 7 of the CONSORT checklist; Box 1) is too large for available resources. Strategies to determine whether the trial question(s) can be answered with fewer subjects are needed. These include: focusing on higher-risk subjects; using a run-in phase before randomisation; "expanding" the primary study endpoint; or running the trial for a longer period, with an event-based, rather than a calendar-based, stopping rule. Choosing subjects with higher riskIf the subjects in a trial have a very low risk of the condition that the intervention is hypothesised to prevent, the trial, regardless of sample size, will not prove the value or otherwise of the intervention. For example, in the "Finnish Businessmen's Study", the efficacy of a multifactorial risk-factor intervention to prevent cardiovascular death among middle-aged men could not be proven, as only five such deaths had accrued at the end of the scheduled follow-up.2 The proof required from trials relies on demonstrable differences in event counts between the intervention and control groups, and whether this difference could reasonably have occurred by chance alone. It matters little how many subjects produced these event counts — the evidence rests in the main with the event counts themselves and the size of the difference between them. Consequently, if the calculated sample size of a proposed clinical trial is larger than feasible, limiting the subjects to those in a higher-risk category should be considered. In the Finnish Businessmen's Study, it might have been better to recruit only men with prior heart disease, with four to eight times the risk of those in the primary prevention category. Similarly, in trials to prevent cancer recurrence after initial therapy, focusing on individuals with above-average risk of recurrence would require a smaller sample size. At times, however, the cost and feasibility advantage of using a lower sample size might be outweighed by the extra time and effort needed to identify high-risk individuals. This might occur especially where the features determining higher risk are not clinical characteristics, but are based on medical testing. In Box 2, a comparison of two possible trials shows that Trial B, with a similar study power, is more feasible and presumably less costly than Trial A. Maximising study power through better compliance — use of a "run-in" design In a clinical trial design, a "run-in" phase can reduce the required sample size.3 Subjects who are entering a long-term trial are asked to take the study medication(s) for a period before randomisation. Individuals who lose interest early on (potential "drop-outs") can then be excluded before random allocation. Similarly, any subjects who feel they may have an indication to receive the intervention treatment (potential "drop-ins") can also withdraw before randomisation. This potentially lowers rates of anticipated non-compliance to allocated treatment during a trial, resulting in a smaller required sample size. As the calculated sample size is exquisitely sensitive to compliance, this procedure can be of major benefit (Box 3). (Once randomised, these participants would generally be included in an intention-to-treat analysis4 and only dilute the apparent effect of the intervention, boosting the sample size needed and/or follow-up duration.) Run-in phases can use either placebo or active therapy, and are usually single blind (ie, only the study staff are aware of the nature of the medication). A placebo run-in allows trial staff to be sure that reported side effects are not caused by treatment (colouring agents and excipients in placebos can occasionally cause reactions), whereas an active run-in can identify and exclude individuals who may be unable to tolerate the medication being tested in a long-term trial. In the US Physicians Study (testing the value of aspirin to prevent coronary death and β-carotene to prevent cancer), a placebo run-in phase allowed a trial of 22 000 doctors to deliver comparable results to a trial requiring 33 000 doctors, assuming that doctors who withdrew during the run-in period would otherwise have stopped taking the study medication soon after randomisation.3,5 Whether excluding any potential trial subjects in this way will reduce the generalisability of the ultimate trial results needs to be carefully considered. Choosing a different endpoint to limit the sample sizeIf a more frequently occurring endpoint can be substituted, with the same biologically anticipated effects of treatment, then the required sample size will fall accordingly. For example, while trials of lowering cholesterol level to reduce total mortality over 5 years may require, say, 12 000 patients, similar trials to reduce coronary mortality only (which cause a fall in total mortality) may only need 8000 patients, depending on the proportion of deaths due to coronary causes. Furthermore, trials designed to reduce the combined endpoint of coronary death plus non-fatal myocardial infarction may require perhaps 4000 patients, with even fewer required for trials designed to reduce all vascular events (all cardiovascular deaths plus non-fatal myocardial infarction plus non-fatal stroke plus any revascularisation procedure). Of course, in the above example, as the endpoint becomes broader, "softer" clinical outcomes are included (ie, some outcomes, such as a decision to send a patient for a revascularisation procedure, may be more subjectively based, and even influenced by a patient's treatment, including the study treatment, if blinding has failed). The decision as to the choice of the primary endpoint in trials should be made in consultation with the clinicians who will ultimately use the trial's outcomes in practice. Selection of the endpoint must ensure that sufficient information is available to determine whether the new treatment should be applied in clinical practice.1 In any case, tracking (which is blinded to study treatment) of the risk profile of subjects randomised into a clinical trial should occur during recruitment, as well as monitoring during follow-up (also blinded) of the event rates in the entire cohort to allow consideration of a possible increase (or, rarely, decrease) in the target sample size before the end of recruitment; a change in the primary outcome of the study; and extending the scheduled follow-up period to yield more events. Whenever possible, it is important to specify a stopping rule in the study protocol, based on accrued numbers of events rather than a calendar date, to allow a trial to continue without major disruption when trial outcome risks are lower than expected. Buying extra science for little extra cost — substudies in large clinical trialsOnce a study outline has been finalised, formal consideration should be given to substudies nested within the larger trial. The use of surrogate outcomes offers the opportunity to answer questions of related interest, or to explore the mechanism of the treatment effect6 in ways which might otherwise be prohibitively costly (ie, setting up substudies as separate enterprises). For example, in a study of the effects of lipid-lowering therapy on coronary death and stroke in many thousands of subjects with prior cardiovascular disease, substudies exploring the effects of treatment on (i) the measured progression of coronary atherosclerosis (using serial coronary angiography), (ii) the progression of carotid intima media thickness, (iii) the change in brachial vascular reactivity (using serial ultrasound examinations), or (iv) endothelial vasoactive peptide levels, may have sufficient power with only several hundred subjects each. For each substudy, the resources needed for subject identification and recruitment, running trial clinics and follow-up are already largely covered by the main trial infrastructure, resulting in extremely cost-effective research opportunities. ConclusionA number of strategies can help to ensure that clinical trials research can be done within limited budgets and by smaller-scale collaborations (Box 4). Care must be taken, however, to deliver results that are still meaningful to clinicians, and have a low risk of false-negative conclusions. As always, seeking professional advice can help to ensure success. 1: CONSORT checklist of items to include when reporting a trial1 Section and topic Item no. Descriptor Methods Sample size 7 How sample size was determined and, when applicable, explanation of any interim analyses and stopping rules 2: Comparison of two possible trials — Trial A, with lower-risk subjects, and Trial B, with higher-risk subjects — to determine the value of the same treatment hypothesised to reduce events by 25% (ie, relative risk [RR] = 0.75) during follow-up* Trial A – lower risk (n = 2000) Trial B – higher risk (n = 1000) Treatment group Control Active Control Active Number of subjects 1000 1000 500 500 Proposed RR with treatment 0.75 0.75 Expected event rate 20% 15% 40% 30% Expected number of events 200 150 200 150 Study power at 2P = 0.05 82% 90% * The number of events, rather than the number of subjects, principally determines the power of the study, although the number of subjects determines in part the reliability of each event count and of the difference. 3: Possible effect of a "run-in" design on the sample size of a randomised trial Trial scenario Required sample size A: 100% compliance in both trial arms 400 B: Average of 80% compliance in active arm (ie, 20% drop-outs at study mid-point) 625 C: Half (10%) of the average long-term non-compliers (drop-outs) instead withdraw during run-in phase before randomisation 494 D: Average of 80% compliance in both study arms (ie, 20% drop-ins plus 20% drop-outs) 1110 E: Half the average long-term non-compliers (10% drop-outs plus 10% drop-ins) instead withdraw during run-in phase before randomisation 625 4: Checklist for managing sample size demands in clinical trials Determine the risk profile of the intended population of interest. Can a subpopulation at higher risk readily be found? Determine whether the study design will accommodate either a placebo or an active run-in phase? Establish clear guidelines on whether to randomise potentially non-compliant subjects. Determine the clinically justifiable power for the particular trial. Adjust the calculated sample size for the expected level of non-compliance with treatment. If the event rates are small, identify potential outcomes which may provide alternative endpoint(s) for which the event rate is much larger. Ensure that the risk profile of subjects is monitored blinded during recruitment as well as the event rate during follow-up. Where possible, base stopping rules on the number of events rather than the duration of follow-up. Identify related questions which may be investigated using surrogate outcomes on a subpopulation of randomised subjects.

Anthony C Keech FRACP, MScEpid · Val Gebski MStat

In contrast to curative therapies, preventive therapies are administered to largely healthy individuals over long periods. The risk–benefit and cost–benefit ratios are more likely to be unfavourable, making treatment decisions difficult. Drug trials provide insufficient information for treatment decisions, as they are conducted on highly selected populations over short durations, estimate only relative benefits of treatment and offer little information on risks and costs. Epidemiological modelling is a method of combining evidence from observational epidemiology and clinical trials to assist in clinical and health policy decision-making. It can estimate absolute benefits, risks and costs of long-term preventive strategies, and thus allow their precise targeting to individuals for whom they are safest and most cost-effective. Epidemiological modelling also allows explicit information about risks and benefits of therapy to be presented to patients, facilitating informed decision-making.

Danny Liew BMedSc, MB BS · John J McNeil FRACP, PhD · Anna Peeters BSc, PhD · Stephen S Lim BA, BSc · Theo Vos MD, MSc

To the Editor: The recent article by Johnston et al is an important contribution to the small but growing body of literature on the health effects of particulate matter (PM) pollution derived from bush or forest fire.1 The authors studied an important wood smoke PM exposure in Australia and showed consistent associations between higher concentrations of PM and emergency department presentations for asthma. Most research on the effects of PM has focused on motor-vehicle-derived PM pollution.2,3 However, Johnston et al do not appear to have accounted for serial correlation in their data. Measurements connected in time, such as repeated measurements of the same population, are likely to be correlated and not independent.4 Further, school holidays have been shown to influence hospital admission rates.5 The major Northern Territory school holidays in June and July are in the middle of the study period. Johnston et al adjusted for some important confounders in their analysis (acute respiratory infections and weekdays/weekends).1 However, in time-series data, especially those dealing with asthma, serial correlation, as well as other potentially important confounders such as school holidays and temperature and humidity, should also be assessed. It may be that, even after appropriate adjustments for serial correlation and potential confounders, the rate ratios found by Johnston et al may not alter appreciably. However, it would have been useful for the investigators to have at least discussed any effects that controlling for serial correlation and other potential confounders might have had on their findings.

Bin B Jalaludin · Guy B Marks · Geoffrey G Morgan

In reply: Jalaludin and colleagues query the potential effects that serial correlation and confounding by school holiday time periods may have had on our finding of an association between particulates derived from bushfire smoke and asthma presentations.1 As previously discussed by Schwartz, time series analyses are important to control for serial correlations, particularly those due to the effects of seasonality and weather fluctuations.2 Our study did not cover a number of seasons. It was conducted during one tropical dry season, a period characterised by remarkably stable day-to-day weather conditions.3 For this reason, we believe that the effects of any autocorrelation would have been negligible. It is of interest that the development of statistical methods for analysing time series of count data during the 1990s, and analysis of large studies of particulate pollution using these methods, did not have an important effect on the conclusions reached by earlier studies.4 There is evidence that hospital admissions for asthma fall during school holidays.5 Anecdotal reports of more regional fires suggest that, if anything, particulate concentrations over Darwin might increase at these times. A reanalysis of our data including school holiday periods as a potential confounding factor did not appreciably alter our results in either the continuous (revised incidence rate ratio [IRR],1.26; 95% CI, 1.12–1.41, compared with original IRR, 1.20; 95% CI, 1.09–1.34) or categorical analysis (see Table). Asthma presentations and exposure levels of PM10* (μg/m3) Rate ratio for asthma presentations (95% CI) Same-day PM10 category (μg/m3) Original analysis† Revised analysis‡ < 10 1.0 1.0 10–< 20 0.90 (0.60–1.35) 0.84 (0.43–1.63) 20–< 30 1.11 (0.74–1.69) 1.13 (0.58–2.18) 30–< 40 1.18 (0.72–1.97) 1.21 (0.58–2.50) ≥ 40 2.38 (1.46–3.90) 2.47 (1.21–5.01) * Particles of 10 microns or less in aerodynamic diameter per cubic metre. † Adjusted for influenza-like illness and weekday. ‡ Adjusted for influenza-like illness, weekday and school holiday periods.

Fay H Johnston · Anne Kavanagh · David MJS Bowman · Randall K Scott

To the Editor: In an article in the 1 April issue of the Journal,1 Sturm et al reported on a GP-based stroke audit ("ASAP") and stated that "the information obtained is likely to be representative of most Australian general practice environments". Without further information, we cannot be as confident. First, their sampling strategy was unconventional. Of all registered GPs from five Australian States and one Territory who were initially approached in May 2000, only 10.2% (n = 1850) of eligible GPs expressed interest in participating in the study. From each of 22 "geographical regions", up to 18 GPs were recruited, initially by random sampling and then by replacement, to obtain a sample of 396 GPs, of whom 321 (81%) provided data. No GP data by State and Territory or "geographical region" were provided to allow readers to judge the possibility of sampling bias. Unpublished data from our own GP survey about stroke issues in New South Wales raise this possibility. We conducted a postal survey of 490 randomly selected GPs from November 2000 to February 2001 (response rate, 60%). None of the 296 participating GPs stated they were enrolled in a stroke clinical audit. Second, although patients were clustered within GPs, no intracluster correlations (ICCs) were reported. Outcomes (eg, disease morbidity and risk factors) for patients recruited from general practices tend to be correlated at the GP level.2 ICCs quantify the extent to which individuals within clusters (such as a GP's practice) are similar to each other relative to individuals from other clusters. Conventional formulas for calculating confidence intervals assume that the ICC is zero (ie, no clustering). Yet, where correlation within clusters does exist (ie, ICC > 0), the effective sample size is reduced and the associated CIs are inevitably wider. For any given ICC greater than zero, larger cluster sizes also further reduce the effective sample size. Applying appropriate formulas,3 we calculated effective sample sizes for risk factors in the ASAP study, assuming three different magnitudes of ICCs, ranging from relatively modest (0.015) through more substantive (0.1) (see Box). Given the large denominator of the ASAP study, our methodological concern may be only minor in terms of the width of the CIs reported, but the reader is unable to judge whether or not this is the case, as no ICCs were reported. As sample-size calculations for future interventional studies would be informed by publication of ICCs,4 we encourage such reporting in future. Third, we believe the authors' quantitative findings would have been most useful if they had been age-adjusted in line with Australian community norms. Effective sample size, assuming three different magnitudes of intracluster correlation (ICC) Risk factor Actual n Effective n if ICC = 0.015 Effective n if ICC = 0.05 Effective n if ICC = 0.1 Total Hypertension 14 280 8643 4499 2670 Hypercholesterolaemia 12 516 7973 4317 2608 Smoking 14 297 8649 4500 2670 Diabetes 13 767 8455 4449 2653 Atrial fibrillation 14 194 8611 4490 2667 Stroke/transient ischaemic attacks 14 321 8657 4502 2671

Sandy Middleton · Neil J Donnelly · Jeanette E Ward

In reply: We thank Middleton et al for their interest in our article. As 96% of questionnaires in our ASAP study1 were completed by September 2000, their study (as yet unpublished) and ours were not concurrent. Statistically, based on the information given by Middleton et al, we would expect 5.5 GPs (296 x 333/18066) to be involved in both studies. Chance, or because direct involvement in the ASAP study had finished months earlier, may explain why none of the doctors in the survey by Middleton et al stated that they were involved in a stroke audit. In answer to the claim that "no GP data by State and Territory" were provided, we did in fact indicate in our article how many GPs from each State and Territory participated. Intracluster correlations (ICCs)2 for each risk factor in our study are shown in the Box. ICCs have a greater effect on sample size than on CIs, because CI width is inversely proportional to the square root of the sample size. The large sample size of ASAP means that the study has acceptable precision, even after allowing for ICCs. Overall estimates for risk factors were provided for the population of people consulting GPs, which is the relevant population. We would not necessarily expect the same distribution of risk factors in people not attending GPs. Age- and sex-specific risk-factor prevalences, shown in Box 3 of our article,1 can be used to calculate age- and sex-standardised rates for any desired population. We are confident that the information obtained in our study is likely to be representative of most Australian general practice environments. Intracluster correlations (ICCs) for stroke risk factors in the ASAP stroke audit1* Risk factor All Men Women Current smoker 0.07 0.09 0.08 Hyper-cholesterolaemia 0.06 0.06 0.07 Hypertension 0.06 0.05 0.07 Diabetes 0.04 0.05 0.07 Past TIA/stroke 0.018 0.024 0.013 Atrial fibrillation 0.016 0.017 0.023 TIA = transient ischaemic attack. * Calculated using the analysis of variance (ANOVA) method.2

Jonathan W Sturm · Stephen M Davis · John G O'Sullivan · Miriam E Vedadhaghi · Geoffrey A Donnan

Sample size must be planned carefully to ensure that the research time, patient effort and support costs invested in any clinical trial are not wasted. Item 7 of the CONSORT statement relates to the sample size and stopping rules of studies (see Box 1); it states that the choice of sample size needs to be justified.1 Ideally, clinical trials should be large enough to detect reliably the smallest possible differences in the primary outcome with treatment that are considered clinically worthwhile. It is not uncommon for studies to be underpowered, failing to detect even large treatment effects because of inadequate sample size.2 Also, it may be considered unethical to recruit patients into a study that does not have a large enough sample size for the trial to deliver meaningful information on the tested intervention. Components of sample size calculationThe minimum information needed to calculate sample size for a randomised controlled trial in which a specific event is being counted includes the power, the level of significance, the underlying event rate in the population under investigation and the size of the treatment effect sought. The calculated sample size should then be adjusted for other factors, including expected compliance rates and, less commonly, an unequal allocation ratio. Power: The power of a study is its ability to detect a true difference in outcome between the standard or control arm and the intervention arm. This is usually chosen to be 80%. By definition, a study power set at 80% accepts a likelihood of one in five (that is, 20%) of missing such a real difference. Thus, the power for large trials is occasionally set at 90% to reduce to 10% the possibility of a so-called "false-negative" result. Level of significance: The chosen level of significance sets the likelihood of detecting a treatment effect when no effect exists (leading to a so-called "false-positive" result) and defines the threshold "P value". Results with a P value above the threshold lead to the conclusion that an observed difference may be due to chance alone, while those with a P value below the threshold lead to rejecting chance and concluding that the intervention has a real effect. The level of significance is most commonly set at 5% (that is, P = 0.05) or 1% (P = 0.01). This means the investigator is prepared to accept a 5% (or 1%) chance of erroneously reporting a significant effect. Underlying population event rate: Unlike the statistical power and level of significance, which are generally chosen by convention, the underlying expected event rate (in the standard or control group) must be established by other means, usually from previous studies, including observational cohorts. These often provide the best information available, but may overestimate event rates, as they can be from a different time or place, and thus subject to changing and differing background practices. Additionally, trial participants are often "healthy volunteers", or at least people with stable conditions without other comorbidities, which may further erode the study event rate compared with observed rates in the population. Great care is required in specifying the event rate and, even then, during ongoing trials it is wise to have allowed for sample size adjustment, which may become necessary if the overall event rate proves to be unexpectedly low. Size of treatment effect: The effect of treatment in a trial can be expressed as an absolute difference. That is, the difference between the rate of the event in the control group and the rate in the intervention group, or as a relative reduction, that is, the proportional change in the event rate with treatment. If the rate in the control group is 6.3% and the rate in the intervention arm is 4.2%, the absolute difference is 2.1%; the relative reduction with intervention is 2.1%/6.3%, or 33%. Estimating the plausible effect of treatment to be sought in a randomised controlled trial provides a further challenge, and may be the most common problem for reported trials. Too frequently, studies are designed to identify an implausibly large treatment effect (for example, a 30% to 50% reduction), when most important treatments that have been adopted into clinical practice have shown more modest benefits. When studies are designed to find unrealistically large reductions and fail, smaller real reductions are inevitably rendered statistically non-significant, leading to confusion about the value of the intervention studied. To resolve uncertainty, the study then needs to be repeated elsewhere, but with a larger sample size than before. Wherever possible, the minimum worthwhile difference in response should be determined from phase II or pilot studies and expert opinion from colleagues. Investigators should take into consideration any cost or logistical advantages or disadvantages of the interventional treatment compared with standard care. From these components, sample size can be calculated as shown in Box 2. It can be seen that the required sample size increases as the chosen significance level becomes smaller and as the chosen power increases. Also, even a small change in the expected absolute difference with treatment has a major effect on the estimated sample size, as the sample size is inversely proportional to the square of the difference. Thus, if 1000 participants per treatment group are required to detect an absolute difference of 4.8%, 4000 per treatment group would be required to detect a 2.4% difference. Precise calculation of sample size for different types of outcomes (continuous, binary and time-to-event) is discussed in standard texts.3-5 A checklist for determining sample size is given in Box 3. Effect of complianceA major limitation of many sample size calculations is the failure to account for patients' predictable lack of compliance with their allocated treatments. As compliance losses directly affect the size of the achievable treatment difference, they also affect the estimated sample size in a non-linear fashion. For example, a placebo-controlled study needing 100 patients per treatment arm, with 100% compliance, would require about 280 patients per arm if compliance is only 80% in each group (that is, 20% of patients allocated the investigational treatment fail to take it, and 20% of patients allocated to the placebo-control arm cross over to the investigational treatment). The compliance adjustment formula is adjusted n per arm equals N/([c1+c2–1]2), where c1 and c2 are the average compliance rates per arm (so, in the above example, adjusted n = 100/([0.8+0.8–1]2) = 280). Allocation ratioA one-to-one allocation to intervention and control treatment arms is the most common form of random allocation and results in the smallest sample size requirement. Sometimes different allocation ratios are chosen, resulting in a larger total sample size needed to achieve the same power. This may be justified where the investigational treatment is unusually expensive or complicated to administer. Reporting the sample size section of the protocolThe sample size calculation should be described in sufficient detail to allow its use in other protocols. The power, level of significance and the control and intervention event rates should be clearly documented. Information on the scheduled duration of the study, any adjustment for non-compliance and any other issues that formed the basis of the sample size calculation should be included. For continuous outcomes, in particular (eg, blood pressure), assumptions made about the distribution or variability of the outcome should be explicitly stated. ConclusionEstimating sample size is important in the design of clinical trials, and the quality of the estimate ultimately depends on the quality of the information used to derive it. Care should be taken to avoid overestimating the likely event rate and the feasible effects of treatment. The objectives and outcome measures of the study must be clearly stated,6 and the information used in calculating the sample size should reflect as closely as possible the type of data that will be gathered from the trial in question. Professional advice should be sought before embarking on any major trial project. 1: CONSORT checklist of items to include when reporting a trial1 Selection and topic Item no. Description Methods Sample size 7 How sample size was determined and, when applicable, explanation of any interim analyses and stopping rules 2: Generic expression for calculating sample size Sample size α (power, inverse function of significance level*) (absolute difference)2 * As the P value becomes smaller, the function of the significance level increases. 3: Checklist for determining sample size for clinical trials Estimate the event rate in the control group by extrapolating from a population similar to the population expected in the trial. Determine, for the primary outcome, the smallest difference that will be of clinical importance. Determine the clinically justifiable power for the particular trial. Determine the significance level or probability of a "false positive" result that is scientifically acceptable. Adjust the calculated sample size for the expected level of non-compliance with treatment.

Adrienne Kirby MSc · Val Gebski MStat · Anthony C Keech FRACP, MScEpi

Statistical methods in medical research. 4th edition. P Armitage, G Berry, J N S Mathews. Oxford: Blackwell Science, 2002 (xi + 817 pp). ISBN 0 632 05257 0. The chance of reviewing the new edition of this classic text came just at the right time, as my first edition copy had finally started to disintegrate. My introduction to medical statistics, or indeed any statistics apart from a brief encounter with experimental error assessment, came with the opportunity to sit in on Peter Armitage’s lectures at the London School of Hygiene and Tropical Medicine in 1971. These lectures formed the basis of his book, and since then each edition has improved and expanded considerably on the last, keeping pace with the ever-changing field of medical statistics and adding new co-authors on the way. The book has been reorganised since the last edition, including, among other changes, new sections on permutation and Monte Carlo methods, non-linear regression and multilevel modelling, and also expanding the sections on Bayesian methods and clinical trials. This book is about methods and their application and is aimed at the practitioner, but it is also suitable for anyone with an interest in statistics. It could be read as a unified text and could form the basis of a practice-oriented course, but it is most likely to be dipped into as required. The subject index appears extensive and exhaustive. There is also an excellent author index which helps to track down the context of any of the wide-ranging set of references. The authors do not present any mathematical theory; rather, they concentrate on commonsense explanation and justification for the techniques and methods that they describe, and these are accompanied by plenty of worked examples. They also direct readers to appropriate statistical software. This book belongs on the shelf of anyone who uses or needs to understand anything about medical statistics, and will be constantly on loan from library shelves. Nicholas H de KlerkTVW Institute for Child Health Research Perth, WA

Nicholas H de Klerk

To the Editor: Consensus exists that the provision of medical advice must be based on the correct interpretation of the evidence base. It is logical to assume that consideration should also apply to the provision of medical opinion in cases of medical litigation. The recent article on Sharp v Port Kembla RSL Club1 raises concerns which require wider debate. It is not our purpose to discuss legal niceties nor to contest the epidemiological evidence of an increased incidence, in active smokers, of cancers at several sites, including the head and neck. Rather, we wish to concentrate on a central conclusion in the report, namely the assertion that ". . . a relationship between exposure to ETS [environmental tobacco smoke] and an increased risk of head and neck cancer . . . is supported by the available epidemiology". The larger2 of the two studies quoted showed a crude odds ratio of 2.4 (95% CI, 0.9–6.8). This result is statistically non-significant. The authors also claimed a dose response between "moderate" and "heavy" exposure of 1.8 (95% CI, 0.5–7.3) and 4.3 (95% CI, 0.8–23.5) for non-smokers and 2.5 (95% CI, 0.9–6.9) and 5.3 (95% CI, 1.8–16.1) for smokers. Statistical interpretation of these results leads to a conclusion of no evidence of an increased risk compared with people who were "never" exposed to ETS. Leaving aside our considerable reservations regarding the overall design and analysis of this case–control study, the data as presented are at best suggestive. Significant doubt must remain regarding the role of ETS in head and neck cancer. That being so, two disturbing issues emerge which merit further debate. Firstly, there is an ethical issue as to whether the requirements for the correct interpretation of the evidence base for medical opinion should be any different in the clinic or the courtroom. Secondly, the judgment in this case highlights a dilemma in clinical practice. A clinician is not expected to practise according to non-significant differences in outcome. But, in the event of litigation, will the courts decide, as in this case, that bigger is better?

Allan O Langlands FRACR, FRACS · Val J Gebski BA, MStat

In reply: Our article1 outlined evidence presented to the Supreme Court of New South Wales. The paucity of epidemiological evidence concerning an association between exposure to environmental tobacco smoke (ETS) and laryngeal cancer (two studies available) was offset by biological plausibility concerning the carcinogenicity of tobacco smoke. To that extent, the epidemiological evidence in question "supported" a clear inference of causality from other data. The views offered by Langlands and Gebski do not alter this consideration, and are otherwise without merit for several reasons. To restrict the inference reasonably drawn from epidemiological data to whether or not statistical significance is achieved is inadequate. To offer an overall conclusion other than one based on all the data (in this instance, both studies) is unsound. To publish imputations concerning a specific study in a context denying right of reply by the authors concerned is unfortunate. To identify an ethical problem predicated only on a perceived discontinuity between evidence accepted by a court and evidence accepted by the medico-scientific community is spurious. The Court in Sharp v Port Kembla RSL Club was provided with vigorous criticism of the epidemiological data. Most of the eight weeks of court time was occupied by a painstaking analysis of this and other causative issues. The Court then made a determination consistent with the medico-scientific evidence. Stewart BW, Semmler PCB. Sharp v Port Kembla RSL Club: establishing causation of laryngeal cancer by environmental tobacco smoke. Med J Aust 2002: 176; 113-116. (Received 18 Mar 2002, accepted 21 Mar 2002) South East Sydney Public Health Unit, Randwick, NSW. Bernard W Stewart, PhD, FRACP, Head, Cancer Control Program, and Professor, UNSW School of Paediatrics. Sir James Martin Chambers, Sydney, NSW. Peter C B Semmler, MA, QC, Senior Counsel. Correspondence: Professor B W Stewart, South East Sydney Public Health Unit, Locked Bag 88, Randwick, NSW 2031. stewartbATsesahs.nsw.gov.au AntiSpam note: To avoid spam, authors' email addresses are written with AT in place of the usual symbol, and we have removed "mail to" links. Replace AT with the correct symbol to get a valid address.

Bernard W Stewart · Peter C B Semmler

To the Editor: Some of the principles underlying evidence-based medicine (EBM)* might have been around far longer than we tend to believe. Here is a fragment of one of the 8777 brief suttas (discourses) collected in the Anguttara-nikaya, or "Collection of the gradual sayings", one of the oldest Buddhist texts. The Buddha preaches to the Kalamas people: Yes, Kalamas, you may well doubt, you may well waver. In a doubtful matter wavering does arise. Now look you, Kalamas. Be ye not misled by report or tradition or hearsay. Be not misled by proficiency in the collections [citing the authority of religious texts], nor by mere logic or inference, nor after considering the reasons, nor after reflection on and approval of some theory, nor because it fits becoming, nor out of respect for a recluse (who holds it) . . . But if at any time ye know of yourselves: these things are profitable, they are blameless, they are praised by the intelligent; these things, when performed and undertaken, conduce to profit and happiness — then, Kalamas, do ye, having undertaken them, abide therein.1 This sutta shows the importance of mistrusting unquestioned tradition, even before the days of odds ratios, cost-effectiveness ratios or confidence intervals. Perhaps the lesson for innovative modern supporters of EBM2 would be to concentrate on higher ideals like "profit" (in the sense of beneficence or prosperity) and "happiness" as the really significant outcomes we should be aiming at. * The decision to send this note to the Journal is, of course, evidence-based. The Medical Journal of Australia (MJA) is second only to the BMJ in publishing the largest number of references indexed under the MeSH term "evidence-based medicine" in English-language journals. On a proportional basis, the MJA is at the top of the list: since November 1996 it has published 125 "EBM" articles out of a total of 2553, while the BMJ has published 248 "EBM" articles out of 14966 (OR, 3.06; 95% CI, 2.44–3.83). Could it be that MJA readers are three times more interested in EBM-related topics than BMJ readers?

Diego Rosselli MD EdM MSc

The CONSORT statement is a checklist and flow diagram developed by an international group of clinical triallists, statisticians, epidemiologists and biomedical editors for reporting randomised controlled trials.1 Item 4 in the checklist relates to interventions (Box 1). The interventions used in a randomised clinical trial should be clearly defined in the protocol and reported in enough detail to be replicated. The control or placebo treatment arms should be described with the same degree of detail as the treatment arms. If the control group receives standard care rather than an intervention, this care must be described in detail, as it may differ between institutions or countries. The characteristics of any placebo (eg, tablet or capsule form, taste) and the way it is administered should be documented. If the study interventions are delivered in a blinded (masked) fashion, details of how the blinding was achieved should be described, including any procedures for unblinding subjects during the study. The use of blinding is desirable to reduce reporting and measurement bias.1 A study is classified as single-blind when only the study subject is unaware of which treatment has been assigned, and double-blind when the responsible clinician is also unaware of the assigned treatment. Double-blind studies, in which data are presented to the data-monitoring committee in a blinded fashion (ie, as treatments A and B), are sometimes referred to as triple blind.2 If blinded interventions are not feasible or ethical, blinded assessment of outcomes should be attempted. For example, in a study comparing psychological outcomes after coronary surgery or percutaneous angioplasty for coronary heart disease, the assessor can still be blinded to treatment if patients are carefully gowned to obscure the presence or absence of a surgical scar and trained not to disclose the type of treatment received (assessments can even be videotaped to check that the blinding is preserved). Pharmaceutical interventionsGenerally, the dose of a drug intervention used in a comparative trial would be the maximum effective tolerated dose determined from earlier-phase trials. The dose may be the same for all patients or modified according to criteria such as body weight or surface area. Alternatively, dose escalation or reduction may be appropriate to achieve a particular degree of response (eg, lowering of cholesterol or raising of haemoglobin levels) or where known side-effects have been reported. In addition to the usual monitoring of patients' details, any special safety investigations required as part of the trial should be reported. For instance, if a medication has been known to cause liver toxicity in some patients, the schedule used for monitoring liver enzymes should be included in the protocol and study report. The description of pharmaceutical interventions should include the generic name, proprietary name (where brand substitution is not allowed), dosage formulation, route of administration, frequency of dosage, duration of therapy and any criteria for dosage modifications or cessation of the intervention during the course of the trial.3 Any special handling procedures and storage conditions should be noted. Non-pharmaceutical interventionsInterventions that do not use drugs, such as surgical procedures and behavioural therapies, are more likely to vary in the way they are administered. It is therefore important to document the aspects of such interventions that were controlled closely by the protocol to enable readers to best ascertain how the intervention differed from their own practice. Similarly, multimodality treatments may follow specific schedules of delivery, and should be detailed in reports.4 How was the intervention received?Some indication of the proportion of patients receiving the interventions and how well these were tolerated should be reported. Poor compliance generally results in an underestimation of the actual benefits of treatment and may even produce a false negative result. Pilot studies can be useful in identifying problems with the delivery of treatments before a major study is initiated. Ancillary careDetails relating to ancillary care and the criteria for providing it should be reported. Some studies stipulate that, except for the intervention under investigation, all other patient care is left to the discretion of the attending clinician. As ancillary care varies depending on the study centre, clinician preferences and patient comorbidities, key details should be documented. Ancillary care may also be specified in the protocol. For example, antiemetics may be used routinely in an oncology trial to allow for a planned fixed dose of a chemotherapy regimen for all patients. Many interventions are used with specified "rescue or salvage options" in the event of treatment failure. Other aspectsStudy sponsors and suppliers of any intervention should be acknowledged and any potential conflicts of interest declared. Documentation that appropriate ethical and regulatory approval has been obtained to conduct the trial is essential. All drugs and devices not listed on the Australian Register of Therapeutic Goods require Therapeutics Goods Administration (TGA) approval for use in a trial under the Clinical Trial Notification (CTN) or Clinical Trial Exemption (CTX) schemes. This also applies to trials evaluating new doses of drugs or indications for approved products. In conclusion, a checklist for specifying interventions is shown in Box 2. 1: CONSORT checklist of items to include when reporting a trial1 Section and topic Item no. Descriptor Methods Interventions 4 Precise details of the interventions intended for each group and how and when they were actually administered 2: Checklist for specifying interventions in a clinical trial Is enough detail provided so that the intervention could be replicated by others? Is the control group intervention described in enough detail? If blinding was used, has this been described and was it maintained? Is background and evidence for choice of dose included? Have criteria for dose modification or cessation of therapy been included? Were additional investigations or non-standard monitoring schedules required to ensure patient safety? Is any evaluation of compliance or tolerance included? Was ancillary care described or specified?

Jackie K Brighton BAppSc, MPH · Val J Gebski BA, MStat · Anthony C Keech FRACP, MSc(Epi)

To the Editor: A recent editorial in the Journal focused on the "blurring of research ideals and corporate interests".1 But there are other funding and commissioning bodies, including government, whose wants or needs also have the potential to blur research ideals and exert control over what can be published. In recent times, those who pay the piper increasingly want to call the tune. Understandably, this is also an issue for research into Aboriginal ill health.2,3 Van Der Weyden's plea for the development of national guidelines on institutional conflict of interest should therefore be broadened to include all funding bodies. One suggestion for inclusion in these guidelines, to enhance public interest in research, is an obligation for authors to state not only their sources of funding, but "the origin of the research question they are attempting to answer"4 and the person or group who initiated the funding of the project.

Max Kamien

Objective: To determine the prevalence of faecal incontinence in the community and evaluate identifiable risk factors.Design and setting: Cross-sectional survey using a validated questionnaire. A short version of the questionnaire was sent to 220 subjects and a long version to 770 subjects, randomly selected from western Sydney, Australia.Main outcome measures: Self-reported faecal incontinence, defined as involuntary loss of anal sphincteric control leading to unwanted release of liquid or solid faeces (not flatus) at an inappropriate time or in an inappropriate place, within the past 12 months. The long questionnaire also sought information on bowel habit and potential risk factors for faecal incontinence.Results: The response rate was 66%. The prevalence of solid or liquid faecal incontinence was 2% and 9%, respectively. The mean age of subjects with faecal incontinence was 53 years; 55% were women. After adjusting for age and sex, there was a significant association between faecal incontinence and perianal injury (P = 0.03), perianal surgery (P < 0.001), feelings of incomplete defecation (P < 0.0001), loose or watery motions (P < 0.0001) and urgency (P < 0.0001). Seven of 48 subjects with faecal incontinence reported being asked by their physician about faecal incontinence and nine of 33 reported seeking medical advice for their incontinence. Subjects with faecal incontinence perceived their health to be significantly poorer than did other subjects (P = 0.02).Conclusion: There is a high burden of faecal incontinence in the community, and the prevalence in men may be greater than is usually appreciated. Despite significant associated morbidity, most cases of faecal incontinence were unrecognised by doctors.

Jamshid S Kalantar MB BS, FRACP · Stuart Howell BA(Hons) · Nicholas J Talley MD, PhD

To the Editor: The recent creation of the National Institute for Clinical Studies (NICS) is an exciting new opportunity for bridging the gap between evidence and practice.1 In carrying out this task, NICS will be directed by the members of its Board. Balanced stakeholder representation on the Board is required for NICS to produce optimal results. At present the Board consists of nine members, of whom eight are medical practitioners. The importance of doctors in the process and implementation of quality improvement initiatives is indisputable. However, other healthcare professionals also play a central role in achieving quality health outcomes for patients.2 Board membership more representative of its stakeholders would provide NICS with a broader range of perspectives, which could only be seen as beneficial. Given the current debate surrounding ethics and evidence-based healthcare, the values and expectations of healthcare consumers also need to be taken into account.3 One of the definitions of quality in healthcare is "consistently meeting or exceeding informed customers' opinion".4 It is crucial that the consumer's voice be heard in matters relating to healthcare research and in the implementation of quality initiatives. As the relevance and acceptability of quality initiatives undertaken by NICS will have an impact on health outcomes for consumers, it is important that such initiatives take into account the preferences of consumers. For this reason, we believe it is imperative that NICS include a consumer on its Board. An example of successful integration of a wide range of stakeholders onto a board is the Federal Government-funded National Health Priority Action Council, with representation from State/Territory, Indigenous and consumer groups and a balanced gender mix. We hope that NICS has strategies in place to enhance stakeholder representation on its Board, as this may be a factor in determining whether or not NICS becomes another forgettable acronym.

Louise V Hall

In reply: The Board of the National Institute of Clinical Studies (NICS) agrees strongly with Hall and Lauder that closing the gap between evidence and practice involves input from consumers. We also agree that the Board of Directors should seek to incorporate input from consumers in its strategic and operational activities. Of equal concern to the Board is ensuring the input of other stakeholder groups also currently not reflected in the composition of Board membership. For example, nursing and allied health professions comprise about 80% of the healthcare workforce and have shown strong leadership in relation to evidence-based practice. We are keen to see such groups actively involved in all aspects of the Institute's work. As a Federal Government-owned company, the selection and appointment process for Board members is the responsibility of government and our constitution does not allow the Board to change its own membership. However, the Board is seeking input from both consumers and other key stakeholder groups, both through its initial consultation processes and through establishment of Board advisory groups specifically focused on consumer issues and nursing and allied health. These groups will provide direct and valued input into the strategic and operational activities of the NICS. Our first round of consultation, with over 300 organisations, highlighted a number of areas where there are currently major gaps between evidence and practice, such as cardiac failure, various forms of cancer treatment, prevention of deep vein thrombosis in hospitalised patients, prevention of bedsores, and prescribing of psychotropic drugs for children. We are now examining ways in which the NICS might usefully help in some of these areas to identify barriers and possible solutions that can be rolled out across the healthcare system and sustained. The success of the NICS in achieving this will depend on the willingness of all stakeholders (including health professionals, consumers and managers) to work together in a constructive way.

Louise V Hall BPhty · Allison E Lauder BSc(Nut), MND · Chris A Silagy

Viewpoint Truth in clinical research trials involving pharmaceutical sponsorship Large clinical trials are expensive to mount. Funding comes mainly from pharmaceutical companies seeking information on drug efficacy and adverse events. Patients should be informed of the financial and publication agreements reached between those conducting the trials. This is unlikely to have a significant effect on trial participation and will provide patients with information relevant to informed consent. A small proportion of monies raised from drug trials could be set aside to fund both a trial register site and further studies on adverse drug reactions. Chris A Commens MJA 2001; 174: 648-649 Intellectual property - Publication bias has consequences - Financial disclosure as part of informed consent - Suggested requirements for drug trials - Is trial information reward enough for the public? - References - Authors' details - - More articles on Statistics, epidemiology and research design More articles on Ethics In recent years, economic rationalism has forced public institutions to look for non-governmental sources of income and links with industry.1 Our dermatology department needed equipment for which funds were not available from the hospital budget, but would be available from payment for participating in a drug trial. The trial sponsors wished to compare their product with the current "best" cream and a placebo in a randomised controlled trial. Participation would be voluntary, the risk of harm minimal, privacy would be protected and patients would be "suitably informed". An administrative and financial agreement was arranged between our department and the professional contract research organisation responsible for the study. Details of this trial are shown in the Box. There was some pressure for quick approval, as doctors working from their private rooms had an impressive head start and were already entering patients in the trial. Our institutional ethics committee sought a number of changes to the trial protocol, but it was eventually approved. We had no sooner entered patients into the trial than it was closed: the required number of patients had been supplied by private practitioners. Was this a case of a public institution being too slow in responding to the demands of industry? Perhaps, but there were other, more important issues, particularly those relating to restrictions of intellectual property, the opportunities for publication bias and informed consent of patients in clinical trials. Intellectual property The rights to the information gathered by the drug trial were legally under the control of the contract research organisation. It is likely that many patients enter drug trials believing that the resulting knowledge will be available for the common good. Would the public readily enter similar trials if they knew the intellectual property was controlled by the sponsors and may not be available for the public record? Commercial sensitivity, the complexity of running multicentre trials and timing of publication demand some flexibility, but an insistence on public record of all trial results should be non-negotiable. Publication bias has consequences My concerns about publication bias are shared by others,2,3 and are as follows: If the findings remain the property of the sponsor, then how much evidence is never reported? How truthful is medical evidence that relies on publications selected by an industry which needs to sell new drugs or variations on existing drugs ("me-too" drugs)? "Me-too" drugs require clinical trials showing some advantage, and these trials may be designed with marketing strategies as the driving hypothesis. Trials that show no difference or no effect, or even adverse effects, are less likely to be published, while positive results are likely to be published and promoted. Pharmaceutical companies have to make a profit or they fail.4 There is evidence for selective publication of drug trial information,5 and even manipulation of information6 and opinion.7,8 Publication bias may result in unsafe or more expensive therapies being used. Health resources are limited and inefficient use results in rationing elsewhere. We need all available information to be on the public record to inform us in clinical decision-making. Financial disclosure as part of informed consent Recent judgments in the Australian justice system suggest that informed consent should involve disclosing all issues that might be significant to the patient making the decision.9 Patients may enter drug trials as part of an ongoing doctor-patient relationship, and this may make them feel more secure in the rigours and supervision imposed by trial conditions.10 Patients' trust in doctors is based on the belief that it is their health that remains the central focus. Full disclosure of financial interests might disturb this trust, particularly in trials conducted in private clinics with financial payment made directly to the medical investigator. In public institutions money gained from trials is not usually paid directly to doctors. Generally, most of it is spent on acquiring necessary equipment or to support further research — something likely to be supported by the public. Disclosing trial financial details to patients will create additional difficulties, but truth is more important than false trust. The Royal Australasian College of Physicians' Ethical guidelines in the relationship between physicians and the pharmaceutical industry11 and the National Health and Medical Research Council's National statement on ethical conduct in research involving humans12 state that there should be disclosure to research participants of relevant aspects of the budget. More recently, financial disclosure in clinical trials has come under scrutiny in the media.13,14 If we don't ensure such disclosure, then either the political or judicial system might impose it on us. Suggested requirements for drug trials We have progressed a long way in the ethical review of research. However, ethics committees also have increasing workloads and diminishing budgets. They are not necessarily equipped to obsessively interrogate and supervise all submitted projects.15,16 I propose that trial submission forms to ethics committees have two or three further questions confirming a commitment to publish trial results17 and to disclose financial details. This would flag this requirement to both researchers and the industry. Some ethics committees may already have these requirements. The resulting transparency would increase public trust in clinical trials, which, in turn, might make patients more likely to volunteer, ensuring wide and valid representation of different trial subjects. Is trial information reward enough for the public? In entering drug trials the public are risking more than the pharmaceutical industries and the investigators. We all agree that clinical trials are necessary and that, in the right setting, they provide information on new and effective therapies. However, there are other rewards that could be offered to the public. Ready public availability of information on the risks of pharmaceutical products would be an appropriate reward. It is estimated that 80 000 Australians are admitted yearly to Australian hospitals with adverse reactions to pharmaceutical products.18 A proportion of drug trial monies could be dedicated to the study and education of adverse drug reactions. Another proportion of drug trial monies could be dedicated to funding a trial register site17 to provide abstracts of all clinical trials and their results. Finally, we need to examine how and by whom clinical trials are conducted as they are taken from academic medical centres into other sites.3,19 Public institutions are the most protective environment for the public for pharmaceutical and biotechnology trials, provided they have transparent and available guidelines on their interactions with the pharmaceutical industry.20-23 References Health and Medical Research Strategic Review. The virtuous cycle. Working together for health and medical research. Canberra: Canberra Info 1999. Chalmers I. Underreporting research is scientific misconduct. JAMA 1990; 263: 1405-1408. Bodenheimer T. Uneasy alliance — clinical investigators and the pharmaceutical industry. New Engl J Med 2000; 342: 1539-1544. Angell M. The pharmaceutical industry — to whom is it accountable? New Engl J Med 2000; 342: 1902-1904. Rennie D. Fair conduct and fair reporting of clinical trials. JAMA 1999; 282: 1766-1768. Hailey D. Scientific harassment by pharmaceutical companies: time to stop. CMAJ 2000; 162: 212-213. Weatherall D. Academia and industry: increasingly uneasy bedfellows. Lancet 2000; 355: 1574. Larkin M. Whose article is it anyway? Lancet 1999; 354: 136. Rogers v Whitaker (1992) 175 CLR 479. Chalmers I. What do I want from health research and researchers when I am a patient? BMJ 1995; 310: 1315-1318. Royal Australasian College of Physicians. Ethical guidelines in the relationship between physicians and the pharmaceutical industry. Sydney: The College, 2000. National statement on ethical conduct in research involving humans. Canberra: National Health and Medical Research Council, 1999. Pyle G. The drug-body snatchers; No cure, Mrs James, but thanks for all the money; Playing patients in the fast lane; It's the money they have to have. Sydney Morning Herald 13 Feb 2001: 1,4. Pyle G. Patient drug tests enrich hospitals; Vulnerable used as guinea pigs but who guards the guardians? Sydney Morning Herald 14 Feb 2001: 1,4. Savulescu J, Chalmers I, Blunt J. Are research ethics committees behaving unethically? Some suggestions for improving performance and accountability. BMJ 1996; 313: 1390-1393. Wise P, Drury M. Pharmaceutical trials in general practice: the first 100 protocols. An audit by the clinical research ethics committees of the Royal College of General Practice. BMJ 1996; 313: 1245-1248. Scroccaro G, Venturini F, Alberti C, et al. Registering clinical trials. BMJ 2000; 320: 1339. Roughead E, Gilbert A, Primrose J, Sansom LN. Drug related hospital admissions: a review of Australian studies published 1988-1996. Med J Aust 1998; 168: 405-408. Angell M. Is academic medicine for sale? New Engl J Med 2000; 342: 1515-1518. Lemmens T, Singer PA. Bioethics for clinicians: 17. Conflict of interest in research, education and patient care. CMAJ 1998; 159: 960-965. Emanuel EJ, Wendler D, Grady C. What makes clinical research ethical? JAMA 2000; 283: 2701-2711. Boyd EA, Bero LA. Assessing faculty financial relationships with industry. A case study. JAMA 2000: 284: 2209-2214. DeAngelis C. Conflict of interest and the public trust. JAMA 2000; 284: 2237-2238. Authors' details Department of Dermatology, Westmead Hospital, Sydney, NSW. Chris A Commens, MB BS, FACD, Director. Reprints will not be available from the author. Correspondence: Dr C A Commens, 20 Hillcrest Road, Pennant Hills, NSW 2120. ccommensATmail.usyd.edu.au Make a comment Details of the proposed trial Trial: Phase IIb double-blind, placebo-controlled, parallel-group, multicentre study. Aim: Assess the efficacy of topical creams in different bases. Duration: 12 weeks, with five assessment visits. Procedures: Evaluation and count of lesions and assessment of tolerance of treatments. Patient numbers: 300 patients throughout Australia. Payment: $1200 per patient who completed the trial. Patient travel expenses: $20 per visit. Back to text

Chris A Commens