Statistics

Objective: To identify the causes of the gap in life expectancy between Indigenous and non-Indigenous populations of the Northern Territory and how the causes have evolved over time.Design and setting: Analysis of NT death data over four 5-year periods, 1 January 1981 to 31 December 2000 inclusive. A decomposition method using discrete approximations (Vaupel and Romo) was applied to abridged life tables for the Indigenous and non-Indigenous populations of the NT.Main outcome measures: Contribution of causes of death, grouped according to global burden of disease groups and categories, to the life expectancy gap.Results: The gap between the life expectancy of Indigenous and non-Indigenous people in the NT did not appear to narrow over time, but there was a marked shift in the causes of the gap. In terms of disease groups, the contribution of communicable diseases, maternal, perinatal and nutritional conditions halved during the 20 years to 2000. Meanwhile, the contribution of non-communicable diseases and conditions increased markedly. The contribution of injuries remained static. In terms of disease categories, the contribution of infectious diseases, respiratory infections and respiratory diseases declined considerably; however, these gains were offset by significantly larger increases in the contribution of cardiovascular diseases and diabetes for Indigenous women and cardiovascular diseases, cancers and digestive diseases for Indigenous men.Conclusions: The main contributors to the gap in life expectancy between the Indigenous and non-Indigenous populations were non-communicable diseases and conditions, which are more prevalent in ageing populations. With the life expectancy of Indigenous people in the NT expected to improve, it is important that public health initiatives remain focused on preventing and managing chronic diseases.

Yuejen Zhao PhD · Karen Dempsey BN, MPHTM, MAE

It all depends on compliance Earlier this year, public trust in research was dealt a severe blow when evidence emerged that a renowned Norwegian researcher, John Sudbo, had fabricated and falsified data in articles on oral cancer published in The Lancet and the New England Journal of Medicine.1 This news followed hot on the heels of the exposure of fraudulent research by the Korean stem-cell researcher, Woo Suk Hwang, published in Science and Nature.2 There is no doubt these events are but the tip of the iceberg, as research misconduct is endemic,3 and may well become more prominent as the competitiveness and commercialisation of research escalates.4,5 Currently there is strong public support for research, but this is linked to notions of honesty and altruism, and the ability of researchers to regulate themselves. The public expects that a framework is in place to prevent misconduct and to investigate and punish the perpetrators should misconduct occur. These expectations were aired when the Hall affair was played out at the University of New South Wales in 2001–2003.6 Allegations of research misconduct were levelled at Bruce Hall, a professor of medicine at the university, and a renowned immunologist. The investigation was painfully drawn out, with a legal challenge and at least three inquiries. As it progressed, the media had many field days, the reputation of the university was compromised, and the medical faculty and the university’s council were divided. My editorial published in this Journal soon after the controversial ending of the Hall affair proffered a set of principles for managing allegations of research misconduct (Box).6 It now appears that these principles have been incorporated into policy. The National Health and Medical Research Council, the Australian Research Council, and the Australian Vice Chancellors Committee have recently released for public consultation the second draft of the Australian code for the responsible conduct of research.7 The code outlines comprehensive directives for issues such as research data and record management, the supervision of researchers in training, publication of research, authorship, peer review, conflict of interest and matters related to collaborative research. It stresses the need for research institutions to “establish a climate of open exchange of ideas with peers, mutual cooperation, and respect for academic freedom of expression, in which responsible and ethical behaviour in research is expected.” Furthermore, it requires research institutions to have in place active and formal programs for induction of trainee researchers along with continuous professional development of all researchers in the culture and performance of research, including mentorship and effective research supervision. The more contentious aspects of the code are its details for managing research misconduct. Its definition of misconduct as “deviation from the Australian code for the responsible conduct of research” 7 casts a wide net, and raises the possibility that institu-tions as well as individuals can be guilty of research misconduct. Furthermore, the code’s criteria for misconduct, reflecting current patterns of researchers’ misbehaviour,8 extend well beyond fabrication, falsification and plagiarism. It lists 17 examples of research misconduct, including abusive supervision; failure to declare, avoid or manage serious conflict of interest; and inaccuracy and carelessness in record keeping or in the preparation of grant applications or publications. This new and expanded perspective of research misconduct is welcome, but needs to be debated. When does misbehaviour become misconduct, and is the distinction between the two warranted at all? The code proposes two key players in managing misconduct: an institutional advisor on research integrity, and a designated person. The former is a counsellor on research integrity and a confidant to whom the aggrieved and those with complaints can turn for advice. The latter is the institutional inquisitor empowered to conduct a preliminary investigation as to whether allegations have substance and advise whether to pursue a formal inquiry. And herein lies the rub. The principles previously espoused (Box) recommend this be an external and independent inquiry with statutory power. The draft code allows for this, but also allows an alternative option of an internal inquiry. Is an internal inquiry a good idea? Research institutions, including universities, live in fear of adverse publicity associated with misconduct,9,10 and have an inherent and glaring conflict of interest in pursuing an internal inquiry. The community expects that “justice must not only be done but should manifestly and undoubtedly be seen to be done”. The notion of an institution investigating itself will not go down well with a society afflicted by a mistrust of authority and institutions.11 The code is silent on two requirements which will have to be in place if it is to work at all: compliance and accreditation of research institutions, and the establishment of a national body to oversee and evaluate the handling of research misconduct. The research community has long resisted any interference with its privileged status, but the time for scrutiny of research institutions for compliance with the Australian code for the responsible conduct of research is long overdue. After all, research funding is public money, and the public has every right to expect that research institutions pursue “responsible and ethical behaviour in research”. One way to ensure this is through accreditation, with failure to be accredited placing institutions at risk of losing access to public funding. Currently, the United States and Denmark, Finland and Norway have overarching bodies to oversee and evaluate instances of research misconduct.12,13 In the US, the Office of Research Integrity (ORI) has a mandate that for institutions to receive federal funding for biomedical research, they must investigate all instances of alleged research misconduct. Although the US system is far from perfect, the ORI has been active in helping research institutions to conduct their own investigations. If the institutional investigation is deemed inadequate, the ORI can intervene and initiate its own investigation. The ORI’s substantial power lies in the threat to institutions of the potential loss of federal funding.10,14 This power may sit uneasily with Australia’s broad anti-authoritarian culture and with university autonomy, but the competitive and commercial nature of today’s research, and its limited funding, dictate that such a national body should be explored and debated in the Australian context. The creators of the Australian code for the responsible conduct of research7 are to be congratulated. The code represents the first milestone along the long and tortuous road towards maintaining the integrity of research. The six lessons from the Hall affair6 Allegations of serious scientific misconduct should be dealt with from the start by an external and independent inquiry. The inquiry should have statutory power to investigate and inquire. The inquiry should have sufficient scientific expertise to ensure credibility. To preserve public confidence, the inquiry should aim for the highest degree of transparency and accessibility of the final report. There is a need for uniform processes and procedures for dealing with and adjudicating on scientific research and fraud. There is a need to shift the emphasis from managing misconduct and fraud to preventing them.

Martin B Van Der Weyden MD, FRACP, FRCPA

A recent review shows how much more we need to find out about this important problem Perioperative ischaemic cardiac events include myocardial infarction, cardiac arrest and cardiac death, and are estimated to occur in 2%–5% of patients over 40 years of age.1 Mortality rates associated with perioperative myocardial infarction and cardiac arrest may be as high as 25% and 65%, respectively.2,3 In the Australian context, precise data on the numbers of patients at risk are not available, but with more than 440 000 general anaesthetics performed annually, this is likely to be an issue facing many physicians. A recent narrative review of the problem is therefore of timely importance.1,4 What is the risk of perioperative myocardial infarction? As the review points out, perioperative myocardial infarction may be difficult to diagnose, and often unrecognised. Three studies were identified totalling 1309 patients, with myocardial infarction diagnosed by creatine kinase MB elevations with new Q waves, with or without autopsy or positive pyrophosphate scan evidence. Myocardial infarction was identified in 30 patients (2.3%); notably, more than half of these did not have symptoms or signs. Creatine kinase MB assays may result in false negative and positive results, and troponin assays — the biomarker currently used in the European Society of Cardiology and American Heart Association guidelines for diagnosis of myocardial infarction — are now preferred. However, in the perioperative setting, troponin elevation may also arise from non-cardiac causes such as pulmonary embolism and renal failure, and limitations exist in the specificity of individual assays.5 Further, the pathophysiology of perioperative ischaemic events may differ from the non-perioperative acute coronary syndromes, and these differences may affect risk prediction and treatment. Non-perioperative acute coronary ischaemia results from rupture of an often mild, non-obstructive atherosclerotic plaque and superimposed coronary thrombosis.6,7 Although such plaque rupture and thrombosis is also thought to occur perioperatively, there are other important influences. The perioperative state is associated with activation and release of multiple inflammatory mediators and cytokines, sympathetic nervous system activation and catecholamine release, hypercoagulability, and hypoxia. These contribute to both plaque rupture and thrombosis. Additionally, the perioperative stress state may contribute to increased myocardial oxygen demand, in the setting of reduced oxygen supply from blood loss, hypoxia, and other factors. This adverse environment may be present up to 3 days into the postoperative period.8 How can we assess this risk? Given this propensity for perioperative ischaemic events, individual preoperative risk assessment has been keenly pursued by surgeons and anaesthetists, often resulting in referral to a cardiologist. Two methods are commonly used: clinical assessment, and noninvasive testing. A number of clinical assessment tools have been advised, a commonly used one being the Lee index.9 This defines a number of features of patient history, physical examination, baseline investigations, and proposed surgical procedure. Based on the presence of one to five of these clinical characteristics, patients’ risk can be stratified from 0.4% to 5.4% likelihood of a major perioperative event.9 Noninvasive exercise or pharmacological stress testing, usually with echocardiographic or nuclear imaging, is generally reserved for those at higher risk. In Australia, dobutamine stress echocardiography is a commonly used technique, achieving sensitivity and specificity of 85% and 70%, respectively, for a positive test predicting perioperative events in a meta-analysis,10 with similar results for nuclear imaging techniques.10 However, the relatively modest sensitivity and specificity of these tests mean a number of high-risk patients will be missed, and many with high risk will not have an event. The advice to patients about their risk must also be tempered by whether the planned surgery is elective or should go ahead regardless of the risk. How can we manage this risk? Coronary angiography is often advised for patients assessed to be at higher risk, but there is uncertainty in how to respond to the finding of significant coronary artery disease. Revascularisation — either percutaneous or surgical — has been suggested for patients with high grade coronary stenosis, particularly for widespread disease.11 However, supportive data are scarce; several retrospective studies suggest benefit, but a large recent randomised trial in selected stable patients undergoing vascular surgery showed no improvement in outcomes, and possibly an increased risk of events.11,12 At a practical level, if revascularisation is performed, observational data support delaying non-cardiac operations for at least a month following revascularisation surgery.13 Following coronary stenting, a window of 6 weeks after bare metal stenting is suggested, to allow endothelialisation of the stent struts and reducing stent thrombosis,14 but also reducing the possibility of in-stent restenosis, occurring maximally at 3–6 months.15 There are as yet no comparative data following drug-eluting stents, although these appear less attractive, given that stent-strut endothelialisation takes longer, and combined antiplatelet therapy with aspirin and clopidogrel is likely to be needed for longer, further increasing perioperative bleeding risk if these agents are continued, and increasing the risk of acute stent thrombosis if they are stopped early to allow surgery.16 Perioperative coronary events: risk management strategies for those at increased risk Consider not performing surgery if elective Smoking cessation: can be advised for all patients β-Blockade: some evidence, but disputed Aspirin, nitrates, statins: little evidence Revascularisation: little evidence of benefit, some evidence of harm; a particular problem with drug-eluting stents Similar uncertainty surrounds pharmacological methods of perioperative risk reduction. β-Blockers, by reducing myocardial oxygen demand and blocking sympathetic and catecholamine responses, would seem a logical option. Their use is widely promoted, and included in the joint American College of Cardiology and American Heart Association guidelines for perioperative management.17 However, these recommendations are based largely on two randomised controlled trials: one, a small unblinded study,18 the second, a larger study, which showed no survival benefit for β-blockade assessed on an intention to treat basis.19,20 Further trials are currently underway.20 Use of aspirin or statins also seems appropriate, given their previous efficacy in prevention of non-perioperative events,21 but aspirin may increase the perioperative bleeding risk,22 and statins have not yet shown robust benefit, although this is likely an area for future investigation. How then, should the physician put together what is at times confusing information? Firstly, perioperative ischaemia is relatively common and often unrecognised. Clinical assessment and non-invasive imaging are useful, but far from perfect, in risk stratification. Stopping smoking before surgery is a useful intervention to reduce risk.23 Revascularisation, while often used for patients with angiographically important disease, has little evidence to support it, delays subsequent surgery, and has a number of associated problems. Lastly, while statins, aspirin and β-blockers may appear intuitive and are commonly used, there is likewise little evidence to support these approaches. The review by Devereaux et al1,4 is a timely reminder of how little is known about such an important problem, a call to obtain better data, and a suggestion to discuss the rationale for surgery and its possible attendant risks carefully with patients.

Harry C Lowe FRACP, PhD · Saul B Freedman FRACP, PhD

Simon R Brice,* Marie V Pirotta† * Honorary Research Fellow, † Senior Lecturer, Department of General Practice, University of Melbourne, 200 Berkeley Street, Carlton, VIC 3053. chiro_6AThotmail.com To the Editor: During a recent year-long Primary Health Care Research, Evaluation and Development (PHCRED) research fellowship, we encountered all the usual barriers to undertaking good research (funding, time, etc). While privacy legislation has been reported to adversely affect research,1,2 we were unprepared for the time and cost of dealing with the Health Insurance Commission (HIC — now “Medicare Australia”). Our research involved mailing a survey to Victorian general practitioners. For approved research, the HIC supplies a valuable service in providing representative datasets of randomly selected GPs. This was once a quick and relatively inexpensive process — a boon when conducting research with limited funding. Being the first within our department to use this service since the new privacy laws were introduced, we struck unexpected administrative and financial barriers. To maintain anonymity of potential respondents, research materials (ie, surveys and plain language statements) must be mailed by the HIC. So, all items must first be forwarded to the HIC, from where they are remailed to respondents. This process raises a number of hurdles: materials need to be approved (and altered if required) by the “Privacy” department at the HIC, despite prior approval from a duly constituted university ethics committee; there is a limit of two reminder mail-outs (usual protocols for maximising response rates require up to four mail-outs, and inadequate response rates may render research findings unrepresentative and therefore useless); and each mail-out is sent with the same HIC covering letter. Additional requirements lead to an increase in costs — sending envelopes, surveys and plain language statements in bulk to Canberra (numerous times), printing HIC covering letters, and charges for “preparing business rules, extraction specifications, project manage processes to completion . . .”. The list goes on. We were also charged for extraction of the same dataset again for mailing the reminder letter, as more than 2 weeks had elapsed since the original data extraction. Finally, there is the added time. We estimated this to be around 4 weeks, which is detrimental in a limited fellowship position. While the people we dealt with at the HIC were helpful and professional, the time and expense were almost overwhelming. We respect the need to protect the privacy of research participants. However, the “side effects” of applying the new privacy laws are having an adverse impact on primary health care research. Let this be a friendly warning to all those about to set off down the research path — excessive red tape is no longer the exclusive domain of practitioners.

Simon R Brice · Marie V Pirotta

Contributing to health services research, implementation and effective health policy-making Some of the most pressing issues in Australian health care are not about the efficacy of particular treatments, but rather how health services can be organised to deliver optimal care. Examples of service-related initiatives familiar to most clinicians include: multidisciplinary teams to improve coordination of cancer care; designated trauma centres to optimise management of injured patients; financial incentives to encourage particular services; restricted licences for overseas medical graduates to increase the rural workforce; specialist outreach and telemedicine to improve access in remote areas; clinical audit and review to enhance care quality; and management and prescribing guidelines. Broadly speaking, these represent a spectrum of organisational, financial, regulatory and professional interventions aimed at improving service delivery and achieving best practice. Just as clinicians and patients are concerned with the effectiveness of clinical treatments, policy-makers and the public are interested in the effectiveness of health system interventions. For clinical treatments, questions about “what works” may be best answered using randomised controlled trials and other experimental designs. Those studying the effectiveness of health service interventions, however, face some specific methodological and analytical challenges, and often need to consider other types of designs. Is it possible to randomise communities to receive outreach visits, for example? What are the important outcomes of employing nurse practitioners in remote areas? Can we effectively control for other health service changes, such as closure of a hospital, or loss of staff, that may be unavoidable during a study period? In studies in which the intervention is delivered to a population, but the outcomes are measured in individual patients, how do we take clustering effects into account in the analysis? Australians have contributed to developing appropriate methods (some adapted from economics and social sciences) for addressing such questions in real-world situations. Support for the Australian health services research community has come from the Health Services Research Association of Australia and New Zealand (http://www.chere.uts.edu.au/hsraanz/), established in 2001, the longstanding interest of The Medical Journal of Australia, as well as other organisations, and the Australian and New Zealand Journal of Public Health, Australian Health Review, and a new open-access journal, Australia and New Zealand Health Policy (http://www.anzhealthpolicy.com). Syntheses of available research also contribute to rational health policy-making. The international Cochrane Collaboration maintains systematic reviews in which the research literature on a topic has been identified, selected, appraised and synthesised in a transparent way.1 Such reviews reduce the likelihood of people being misled by research findings, and increase the confidence in what outcomes can be expected from an intervention.2,3 However, reviews of health service interventions differ in that, to be useful for policy-makers and managers, the goal of methodological rigour that characterises Cochrane reviews needs to go hand in hand with an understanding of the challenges inherent in health services research. The Cochrane Collaboration’s Effective Practice and Organisation of Care (EPOC) Group, based in Ottawa, Canada, is dedicated to conducting reviews of interventions designed to improve professional practice and the delivery of effective health services, potentially spanning any clinical area.4 It has already produced 37 reviews on topics such as audit and feedback, discharge planning, hospital in the home, printed educational materials, telemedicine and specialist outreach. A particular focus of EPOC has also been how to broaden the types of included studies beyond blinded randomised trials, while at the same time optimising validity and generalisability. These include designs such as controlled before–after studies and interrupted time series studies. Recognising that evidence for policy-making is not always readily available, the Australian Government has provided for a new partnership between EPOC and the National Institute of Clinical Studies (NICS). The Australian EPOC satellite at the National Institute of Clinical Studies was officially announced at the Cochrane Colloquium in Melbourne on 22 October 2005. NICS is funded by the Australian Government to help improve uptake of evidence into clinical practice, and to use evidence about individual, organisational and system change in designing implementation programs. In addition, free access to the Cochrane Library (and a user’s guide) is available through the NICS website (http://www.nicsl.com.au). The overall goal of the satellite is to assist evidence-based policy-making through systematic reviews of interventions designed to improve health care practice and the delivery of effective health services relevant to Australia and our region. In particular, the satellite aims to: identify and help produce priority EPOC reviews relevant to Australia; support EPOC review activity through training and mentoring of researchers; and foster a culture of evidence-based health policy and knowledge translation by promoting the use of the Cochrane Library, and EPOC reviews in particular. In addition, the Australian satellite will: support the EPOC editorial base in Canada by editing, producing and updating EPOC reviews, especially reviews relevant to rural areas; collaborate with the Australasian Cochrane Centre and the other Australian-based Cochrane groups to further the work of the Cochrane Collaboration in the region; and contribute to the international effort of synthesising research to improve evidence uptake. We hope that the satellite will make an ongoing contribution to Australian health services research, implementation and effective health policy-making.

Russell L Gruen MB BS, PhD, FRACS · Heather Buchan MB ChB, MSc, FAFPHM · Jan Davies PhD, MBA · Alain Mayhew MSc · Jeremy M Grimshaw MB ChB, PhD, FRCGP

If experimental conditions are not optimised, correct interpretation of results is difficult Many people throughout the world use complementary and alternative medicine (CAM). In the United States, for example, a survey of 31 044 adults aged 18 years or older indicated that 36% had used some form of CAM in the previous 12 months.1 This widespread use was one reason why, in 1998, the US Congress established the National Center for Complementary and Alternative Medicine (NCCAM) to conduct rigorous research on CAM practices. CAM includes the use of dietary supplements and other natural products; manipulative interventions such as massage; mind–body approaches such as meditation; energy interventions such as acupuncture; and whole medical systems such as traditional Chinese medicine. NCCAM’s mission includes disseminating authoritative information to the public and professional communities concerning which CAM practices are safe and effective and which are not. The use of dietary supplements and natural products is the most widespread CAM practice in the US.1 Thus, one initial approach taken by NCCAM was to sponsor large trials of supplements using doses representative of those commonly used.2 The rationale included the concern that if the common dose is unsafe, it would be important to alert the public. Moreover, these doses were often used in smaller, less well-controlled studies. However, NCCAM found that this is not an optimal research strategy. As NCCAM defines its priorities and strategies for the next few years,3 we recognise that reinvestigation and optimisation of customary procedures, especially dose, is needed if NCCAM is to make informed statements. Is optimisation of CAM interventions needed?It is tempting to accept that the widespread use of CAM signifies that these interventions, as customarily used, are beneficial and safe, and the only research needed is a confirmatory study of customary procedures. Over the past few years, we have recognised these assumptions are often incorrect, largely because of the placebo effect, publication bias, and the inherent complexity of clinical interventions. The placebo effect refers to psychological or physiological changes associated with inert substances or “control” procedures. Placebo effects can be substantial. In an NCCAM-sponsored study on major depression, sertraline (a drug licensed for treatment of depression) was effective in 49% of patients: 25% had full responses and 24% had partial responses. However, placebo was equivalently effective: 43% of patients responded (32% full and 11% partial).4 In a non-NCCAM study, arthroscopic surgery for osteoarthritis of the knee (a procedure used before then on 34 000 patients per year in the US) was no more effective than sham surgery.5 Given the ubiquity and strength of placebo effects, the effectiveness of some CAM practices, as with some other health treatments, may be, at least partially, due to that effect rather than to specific efficacy of the intervention. Publication bias results in negative studies appearing less often in the literature, so that reviews in some journals give an overly positive view of CAM effectiveness. In addition, the literature is unlikely to be conclusive because the manner in which an intervention is commonly used is unlikely to optimise the many factors that together could make an intervention successful. A good example of the difficulty of making correct choices is that of echinacea for the common cold. People could take echinacea for prevention or for treatment of colds; use any of three Echinacea species; take an extract of the roots, or the stems, or the flowers, prepared by any of three procedures; and use any of at least three doses. It is very unlikely that public use has identified the correct clinical indication and the correct echinacea formulation without these parameters being systematically evaluated. In this situation, even well-designed large trials6 may fail to show efficacy. Lack of efficacy of a CAM modality in a given study, coupled with uncertainty about optimal experimental conditions in that study, creates a serious problem in interpretation, and this has practical consequences. If the negative results pertain only to the particular study conditions, more work can be done in the expectation that a positive result will eventually emerge. If conditions are optimal and the results pertain to the intervention generally, the efficacy of the intervention could be more justifiably questioned. Early “negative” results present a particular challenge for CAM, given that some people are very sceptical of the field in general, and will seize upon early results of such trials as demonstrating that a CAM treatment is ineffective entirely. As we became more cognisant of the difficulty in correctly interpreting studies for which conditions were not optimised, we updated NCCAM’s website to address one of these issues: dose optimisation:7 If there are no data to suggest that the proposed dose is likely to give maximum efficacy, or if there are no data to identify the highest tolerated dose that can be tested, the applicant should evaluate a range of dosages to establish the appropriate dose for the study or clearly explain why the optimal dose cannot be established. Use of a suboptimal dose that is safe but ineffective does not serve the larger goals of the CAM community. Any given study can only draw conclusions concerning the dose that was tested. If that dose proves ineffective, the community may conclude incorrectly that all doses of the intervention are ineffective, and patients will be denied possible benefit from the intervention. Dose optimisation: evaluating a range of dosagesAn approach to dose optimisation is suggested by the idealised dose–response curves in the Box. The dose of the intervention rises from a low-dose X to a mid-dose Y to a high-dose Z. “Response” can be considered in terms either of efficacy or of toxicity. In this example, dose X is too low to result in either efficacy or toxicity. Dose Z is so high that toxicity as well as efficacy is seen. Y is an optimal dose, at which high efficacy but only modest toxicity is seen. These curves should hold for any intervention, not just for biologically active agents. Natural product regimens need to be optimised with respect to dose of material in each pill, the number of pills per day, and the number of days of treatment. Mind–body, manipulative, and other CAM interventions also require optimisation of the dose, frequency, and duration. Meditation, for example, is typically taught in group courses of a given length, with patients told to practise a certain number of times per day. There is little literature on the dose–response relationships between the length of training or the frequency of practice and clinical outcomes. Thus, part of NCCAM’s new strategic plan for mind–body research calls for studies to “optimize the timing, components, duration, and level of mind–body interventions to achieve health benefits”.8 For most interventions, NCCAM considers that the dose that is commonly practised in the community is likely to fall between X and Y and have low to modest specific efficacy. With this assumption, placebo-controlled phase I/II clinical trials of that intervention should start with the customary dose, then increase the dose until high efficacy, a plateau of efficacy, or intolerance in terms of toxicity or patient burden is observed. CAM practices often involve complex botanical substances in which the active ingredient is very dilute, or other interventions that can be time-consuming to deliver or practise. For CAM, “intolerance” could be an inability to swallow more product, drink more tea, participate in more classes, or devote more time to certain behaviour such as meditation, rather than the classic systemic toxicity of conventional drugs. If substantial specific efficacy is seen before intolerance, the conclusion will be that an “optimal” dose of the intervention may have been identified, one that is ready for testing in a larger clinical trial. Only if an optimal dose of the intervention is used can definitive decisions about the effectiveness of an intervention be made. Dose–response relationships for beneficial interventions

Jonathan Berman MD, PhD, FAAP · Margaret A Chesney PhD

There is clear evidence of long-term benefits The Early Breast Cancer Trialists’ Collaborative Group (EBCTCG) 2000 overview of adjuvant systemic treatment trials for early breast cancer has demonstrated clear evidence of substantial and significant reductions in both recurrence and mortality, with follow-up now to 15 years.1 This is the fourth EBCTCG overview of adjuvant systemic therapies, conducted at 5-year intervals since 1985.2-6 The EBCTCG 2000 analysis, based on individual patient data from 145 000 women diagnosed with early breast cancer, involved 194 trials started by 1995 in which chemotherapy and hormonal therapy were evaluated alone and in combination for their effects on recurrence, breast cancer mortality and total mortality. This overview, with data from more trials than the earlier overviews, more patients and more years of follow-up, provided new and long-term information on adjuvant chemotherapy in women aged 50–69 years, tamoxifen duration, combined modality therapy, and cause-specific mortality (Box). What were the benefits?Chemotherapy regimens included single agents or polychemotherapy, either cyclophosphamide, methotrexate and fluorouracil (CMF), or anthracycline-containing regimens, mostly fluorouracil, adriamycin, and cyclophosphamide or substituting epirubicin for adriamycin. Anthracycline-containing regimens of about 6 months’ duration reduced the annual breast cancer death rate by 38% in women younger than 50 years, and by 20% in women aged 50–69 years. Similar reductions in annual recurrence rates were seen. The benefits were largely independent of the use of tamoxifen, oestrogen receptor status, or nodal status. Anthracycline-containing regimens were significantly better than CMF regimens for recurrence (2P = 0.0001 [2P is a two-sided P value]) and mortality (2P = 0.00001). There were insufficient trials involving women older than 69 years (< 5% of women) to reliably determine treatment effects. Hormonal therapies studied were tamoxifen (in most trials), ovarian ablation or ovarian suppression. The 15-year follow-up provided an opportunity to evaluate both early and late effects on recurrence and breast cancer mortality for each modality, given alone or in combination with chemotherapy. With respect to mortality, in women with oestrogen-receptor-positive tumours, 5 years of tamoxifen use reduced the annual breast cancer death rate by 31% and the annual recurrence rate by 40%, independent of patient age, the use of chemotherapy, progesterone receptor status or tumour characteristics. However, there was no advantage for a higher dose of tamoxifen than 20 mg per day. Tamoxifen given for 5 years was significantly superior to 1–2 years of therapy, but the evidence for any effect of continuing tamoxifen for more than 5 years remained inconclusive. With respect to recurrence, a significant trend was seen with increasing reduction of annual recurrence rates with increasing age (40–49 years, 29%; ≥ 70 years, 51%; age trend 2P = 0.05). The overview did not include any trials in which tamoxifen and chemotherapy given concurrently were compared with one modality followed by the other. However, as the benefits of tamoxifen and of chemotherapy were largely independent of whether treatment included the other modality, a mortality reduction of 57% for women younger than 50 years and 45% for women aged 50–69 years could be expected by using both modalities together. Do benefits occur early or late?Most of the benefit of polychemotherapy on recurrence was seen in the first 5 years (absolute reductions of recurrence of 12.5%, 12.4% and 12.4% at 5, 10 and 15 years follow-up, respectively, for women younger than 50 years), whereas the benefit for mortality continued to increase for 15 years (absolute reductions in breast cancer mortality of 4.7%, 7.9% and 10.0% at 5, 10 and 15 years, respectively). The early effect of chemotherapy on recurrence had been well established in the previous overview,6 but the continuing late mortality benefit has only now been established by the longer follow-up. The late mortality benefit was less apparent for chemotherapy in women aged 50–69 years. The pattern of benefit from 5 years of tamoxifen was similar to that seen with chemotherapy for women aged less than 50 years, but was apparent in all age groups. Again, most of the effect on recurrence occurred in the first 5 years (absolute reductions for recurrence: 10.4%, 13.6% and 11.8% at 5, 10 and 15 years), whereas much of the benefit on breast cancer mortality occurred after the first 5 years (absolute reductions of 3.6%, 7.9% and 9.2% at 5, 10 and 15 years). This extended mortality benefit, seen with both chemotherapy and tamoxifen, is striking and suggests that an important number of patients with residual disease after primary therapy are cured of their original tumour by adjuvant tamoxifen or chemotherapy, although they remain at continuing risk of new contralateral breast cancer in the long term. Given the similar pattern for clinical benefits observed for the two treatment modalities, the biological outcomes of their effects at the cellular level may have more in common than has previously been recognised. Ovarian ablation or suppression also had a significant, beneficial effect on recurrence (2P < 0.00001) and mortality (2P < 0.004). The pattern of benefit — an early effect on recurrence and a later effect on mortality — was similar to tamoxifen. However, in contrast to tamoxifen, the effect of suppression or ablation was less in trials where all women also received chemotherapy, perhaps because the chemotherapy also suppressed ovarian function. This question is being addressed in current trials. What were the harms?There were minimal long-term effects of all of these agents on non-breast cancer mortality. Chemotherapy was associated with a small, non-significant increase in mortality from heart disease, leukaemia and lymphoma (0.2%); tamoxifen was associated with a small excess mortality from uterine cancer and pulmonary embolus (0.2%). However, the small increase in non-cancer deaths (a few per 10 000 patients per year) was very much less than the reduction in breast cancer deaths seen for each treatment modality. What are the implications?The data from the earlier EBCTCG overviews have already contributed to widespread changes in practice and a recent fall in breast cancer mortality of around 20% in several developed countries. The findings of the 2000 overview will encourage an even wider use of systemic therapies and should contribute to further reductions in mortality.7 Overall, the most important finding from the 2000 overview is that important practical and biological information is gained from long periods of follow-up. Not only has this overview produced definitive results relevant to breast cancer management but, importantly, it has clearly demonstrated two important biological principles. First, that an early reduction in recurrence rates is invariably followed by a reduction in mortality. Hence, recurrence rate reduction may be an acceptable basis on which to recommend changes in practice before survival data is obtain-able. Second, despite the substantial benefits of 5 years of tamoxifen, 2% of patients continue to have a breast cancer recurrence each year from years 5 to 15 after diagnosis. This is a several-fold greater risk of new breast cancer events than was required for the “high risk” women to be eligible for the tamoxifen prevention trials.8 New strategies for ongoing management of these women should be considered. Further, other questions will need to be addressed by the overview process, including the value of tamoxifen or other endocrine therapies beyond 5 years and addition of a taxane to chemotherapy regimens.9 What are the limitations?The current overview only encompassed therapies used up to 1995, which — although clearly effective — are not optimal for all patients in 2005. The 2000 overview did not involve taxanes (there are now more than 10 000 patients in several trials) or aromatase inhibitors (about 30 000 patients in seven trials).10,11 Nor did it include trials with trastuzumab (Herceptin) for women with tumours expressing HER2.12 However, answers to other specific questions such as the value of long-term aromatase inhibitors and of targeted therapies will likely be based on a smaller number of larger trials rather than an overview of many smaller trials. Many such trials, including the important “SOFT”, “TEXT”, and “PERCHE” trials of different combinations of chemotherapy, aromatase inhibitor and tamoxifen for younger women, as well as trials for older women, and trials of taxanes and of trastuzumab, are being conducted in Australia by the Australian New Zealand Breast Cancer Trials Group through international collaboration. These trials should be the subject of separate meta-analyses, conducted in a timely manner to facilitate rapid dissemination of the results. However, long-term follow-up is a particularly valuable feature of the EBCTCG overviews, and the EBCTCG investigators are pursuing strategies to ensure that data from the 2005 overview will be made available sooner and more widely. Key findings of the Early Breast Cancer Trialists’ Collaborative Group 2000 overview Overview of 194 randomised trials of systemic therapies for early breast cancer started by 1995, including data at 10 and 15 years follow-up. Anthracycline-containing regimens are superior to cyclophosphamide, methotrexate and fluorouracil (CMF). Anthracycline-based polychemotherapy reduced annual death rates by 38% (standard error [SE], 5) for women younger than 50 years, and by 20% (SE, 4) for women aged 50–69 years. Tamoxifen reduced annual mortality rates for oestrogen-receptor-positive tumours in all age groups (31%; SE, 3). Combination therapy with tamoxifen and chemotherapy may produce a larger mortality reduction (45%–57%). Effects on recurrence occur early; effects on mortality occur later. Long-term benefits maintained to 15 years. Long-term non-breast cancer deaths from treatment are a few per 10 000 per year, and are greatly outweighed by the reduction in breast cancer deaths. More rapid data dissemination from overviews is required.

John F Forbes FRACS, FRCS, MS · Jack Cuzick PhD

Randomised controlled trials are often not feasible or not appropriate in palliative care research In evaluating evidence for clinical care, study designs are graded according to their potential to eliminate bias,1 and the most robust evidence is considered to come from randomised controlled trials (RCTs).2,3 However, the reliance on study design as the main criterion for credibility of evidence has its critics,4 as does this view of what constitutes the “best” evidence.5,6 In public health in particular, there is debate about the primacy of the RCT for evaluating interventions and about the tendency to downgrade the contribution of observational studies.7,8 More recently, this debate has moved to emerging research areas, such as palliative care. This discipline urgently requires a wider evidence base, but acquiring this evidence presents particular problems. Evidence in palliative care researchIn palliative care research, methodological difficulties arise because of the complex physical, psychological, existential and spiritual problems faced by patients, families and professionals.9-13 These difficulties include patient recruitment, gate-keeping by professionals (ie, reluctance to enrol patients in research studies), small sample sizes, high attrition rates, rapidly changing clinical situations and limited survival times.10,12,13 Palliative care research often focuses on the effectiveness of services for populations, rather than the effect of treatments on individual patients.9 Trials of palliative care services are almost entirely pragmatic (ie, they compare a new service with current best practice).13 The difficulties in identifying, recruiting and retaining patients mean that study populations often comprise those who are best able to cope and least ill. As palliative care is by its nature holistic and often tailored towards the needs of individual patients (pain relief and improved quality of life), it may be difficult to define the intervention precisely and uniformly. Palliative care is also characterised by a multidisciplinary approach. It can be difficult, and possibly also inappropriate, to isolate an individual intervention from a multidisciplinary approach. In addition, treatments that involve various components, changes in services, and surgical or radiological interventions are harder to deliver in a blinded manner to all concerned. Because treatment packages are the mainstay of palliative care research, the ideal type of RCT is seriously compromised.13 It is also important to reflect on the outcomes that we wish to assess. In general, the outcomes of RCTs are to reduce mortality and morbidity and improve survival.14,15 However, extending life is not the central aim of palliative care services, and duration of survival may therefore be irrelevant. Instead, symptom management and health-related quality of life are important outcomes. The timing of measurements is also crucial for trials, yet timing in palliative care is problematic because of the short time between eligibility and death.13 Furthermore, RCTs have been considered inappropriate or unethical in palliative care.9 They are seldom acceptable to patients and their families, who may not wish to risk reducing the quality of life in their remaining days in a trial with a non-intervention arm. Deliberate withholding of support services from the control group has been deemed unethical,16 and it is difficult for researchers to easily gain control “within ethically defensible limits”.13 For example, the Cambridge Hospital at Home study compared 186 patients randomised to receive up to 2 weeks of 24-hour nursing care when nearing death, with 43 control patients on an intention-to-treat basis.17 Problems included the limited power of the study to show differences, service resource constraint of 2 weeks, doctors not wanting to withdraw a desirable service before a patient’s death, 39% of the intervention group dying before receiving the intervention, and the control group receiving an alternative good nursing service. These problems made it difficult to show the worth of the intervention. A new system for classifying evidenceIt is difficult to grade published studies in palliative care using the traditional taxonomies for levels of evidence. Our recent literature review during the preparation of evidence-based guidelines for palliative care in aged care18 revealed numerous problems; many publications fell into evidence levels III (non-randomised comparative studies) and IV (case series),15 and many of the studies could not have been ethically conducted as RCTs. Consequently, to ensure a consistent, defensible approach to evaluating the available studies, we adapted traditional taxonomies in accord with recommendations of the National Health and Medical Research Council (NHMRC).19 We scored studies for quality of methods used to minimise bias, strength and relevance and, based on these scores, defined two new levels of evidence — qualitative evidence and consensus opinion of experts in the field (Box). Although some may consider these levels of evidence less rigorous, we believe that, given the limitations of the study designs, they are the most appropriate criteria for assessing evidence to guide palliative care practice. Alternative approaches to study designThere have been calls in both public health and palliative care for study designs to incorporate the social, economic and political factors that usually influence the effectiveness of the intervention.4,5,14,20,21 The NHMRC has recognised that clinical practice guidelines may improve health more readily for the relatively health-advantaged than for the relatively disadvantaged, potentially increasing health inequalities.22 In response, the NHMRC has developed a framework for incorporating evidence about socioeconomic position and health into these guidelines.14 The tendency for evidence classified as “best” (based on study design) to have been gathered on simple interventions and from groups that are easy to reach in a population raises issues about its relevance and transferability to other groups. Assessing evidence on multiple dimensions would better allow these issues to be taken into account For example, it has been suggested that evidence on the effectiveness of public health interventions should be assessed on three dimensions, similar to those we devised for palliative care interventions, namely: strength of the evidence, which is determined by a combination of study design (level), methodological quality and statistical precision; magnitude of the measured effects; and relevance of the measured effects to the context in which the intervention is to be implemented.4 A pragmatic approach is recommended when considering the importance of study design relative to the other dimensions.4 Study design should not be seen as synonymous with quality of evidence, as it is only one aspect. There are many useful observational designs, including, in particular, prospective open-label studies.23,24 These have a more realistic methodology for palliative care research, with each patient acting as as his or her own control, and data compared before and after the intervention. For example, the efficacy of ketamine as an analgesic was investigated with a prospective, multicentre, unblinded, open-label audit: 39 patients received a 3–5 day continuous subcutaneous infusion of ketamine, in addition to their existing analgesic regimen.23 Patients who achieved a 50% or greater reduction in mean pain scores were designated responders. The responder rate was 67%. A second trial on 43 patients in eight centres found a responder rate of 51%.24 The authors concluded that such data can be used to inform practice, if input and output data are rigorously recorded, and patients act as their own controls.23,24 Quality improvement methods are emerging as a way of obtaining evidence in palliative care. These methods involve stating an aim, measuring success, and testing possible improvements, for example through a PDSA (“Plan, Do, Study, and Act on new insights”) cycle. These cycles can generate deep understanding of complex systems and make sustainable improvements rapidly.25 Although RCTs have their place whenever possible,10,26 the above alternative designs may offer more feasible research protocols that can be successfully implemented in palliative care. If studies are to be fairly and accurately graded for the development of evidence-based guidelines, a second look at this taxonomy is warranted. Rating system for qualitative evidence This system was devised by the Australian Palliative Residential Aged Care (APRAC) project to classify qualitative evidence.* Studies were scored for: Quality of evidence (quality of methods used to minimise bias): This was assessed with eight questions, each with a yes or no answer (scored as 1 or 0, respectively): Was the aim of the study clear? Was the paradigm (philosophical and scientific approach, such as logical positivistic, qualitative) appropriate to the aim? Was the methodology (overall qualitative approach, such as phenomenological, grounded theory, critical theory) appropriate to the paradigm? Were the methods (eg, sampling, data collection, analysis) appropriate to the methodology? Could the rigour of the study be established? (ie, were the methods explicit and transparent, did researchers make explicit their own beliefs, did the analysis search for “negative” cases?) Did the sampling strategy address the aim? Was the data analysis appropriately rigorous? Were the findings clearly stated and relevant to the aim? Strength of evidence (magnitude of intervention effect): 4 = very high; 3 = high; 2 = low; and 1 = very low. Relevance to APRAC project (relevance of outcome measures and the applicability of the study results to the clinical question): 4 = very relevant; 3 = relevant; 2 = of some relevance; and 1 = of little or no relevance. Studies were classified as: Level QE (qualitative evidence) and were considered appropriate for development into guidelines if they had a quality rating of 6 or higher (out of a total of 8) and both a strength and a relevance rating of 3 or 4 (out of a total of 4). These studies are usually descriptive and include detailed, rich and “integrative” analysis, including observational or case studies. Level EO (expert opinion), if they contained no quantitative or qualitative evidence, but provided information about best practice from an expert or experts in that field, as agreed by the project team. Because expert opinion is generally the result of experiential knowledge, it was considered helpful to the development of the guidelines and, accordingly, was included in the preamble for each chapter. However, as it was not research-based, it was not used as the basis for any guidelines. * The first edition of the APRAC guideline document was made available for public comment.18 This description is based on the second edition, currently undergoing evaluation by the National Health and Medical Research Council.

Samar M Aoun PhD · Linda J Kristjanson PhD

Vietnam veterans reported a high prevalence of health problems among their partners and children in a 1998 survey. Data about the effect of our veterans’ war service on the health of their families are quite limited. These data are mainly from the Vietnam and Gulf Wars; cover veterans, partners and children independently; and largely focus on the individuals’ medical conditions and risk factors. Australia should develop a broad research strategy that uses a wider definition of health, looks at veterans’ families as a whole, and does so from a range of perspectives, including sociological, life-course and trans-generation perspectives. Preventive research should be emphasised, especially into enhancing resilience of veterans’ families. The use and usefulness of current services should be evaluated, including whether they need to be more family-inclusive.

Hedley G Peach PhD, FFPH

To the Editor: Forder et al conveyed that trials without allocation concealment have the potential to mislead.1 However, it is not true in any meaningful sense that “Without exception, allocation concealment is achievable in all randomised clinical trials. In contrast, it is not always possible to blind people to study treatments received.” Rather, “Masking may be defined as either the process (researchers not revealing treatment codes until the database is locked) or the result (complete ignorance of all trial participants as to which patients received which treatments). A masking claim indicates only the former . . . If masking is possible only some of the time, then clearly reference is being made to the result, and not the process. To be fair, then, one would have to ask if the result of allocation concealment is always possible . . . only the process of allocation concealment, but not its result, can be ensured.”2 Forder et al also state that certain methods (including sealed envelopes) are considered to be adequate concealment methods. Sadly, this is true, but only if the emphasis is on the word “considered”, because sealed envelopes are both imperfect at preventing direct observation of future allocations and useless at preventing the prediction of future allocations, even without direct observation. Because the extent of prediction depends on the specific restrictions used on the randomisation,3 allocation concealment is not even a binary phenomenon, and so to truly assess allocation concealment in a given trial, one must ask how much prediction is possible in that trial. Allocation concealment is perfect if no observation or prediction is possible, and only partially effective if some prediction is possible. Many trials use randomised blocks, and smaller block sizes tend to allow for substantial prediction.3-5 So, while methods aimed only at preventing the direct observations of future allocations may be considered to be adequate, it is clear that in reality they are not. That the authors failed to use this opportunity to set the record straight indicates their implicit agreement with the incorrect statement that methods aimed only at preventing the direct observations of future allocations are not only considered adequate, but actually are adequate. Pretending that allocation concealment is binary, and hence that it suffices to use methods aimed only at preventing the direct observations of future allocations, represents ignorance that may be bliss, but certainly is not harmless.

Vance W Berger

To the Editor: In their article on controlled trials, Forder et al1 described the trial by Karlowski et al on vitamin C and the common cold2 as an example of how patients’ or investigators’ preconceptions about the value of the treatment may affect a trial’s results. However, their presentation of this trial is misleading in two respects. Firstly, the Karlowski et al trial was reanalysed and the “placebo-effect explanation” of the original authors was shown to be erroneous.3 For example, their subgroup analysis of “blinded” and “non-blinded” participants excluded 42% of all episodes of colds, even though the subgroups were presented as complementary; numerous further problems are detailed elsewhere.3 Thus, the trial by Karlowski and colleagues cannot be seen as an example of the placebo effect in action. The concept of large and omnipresent placebo effects can be traced back to an early article by Beecher, who chose “15 illustrative studies” covering such conditions as, “severe postoperative wound pain, cough, headache, seasickness, etc.”4 Beecher calculated that the “average placebo-effect” was 35.2% (SE, ± 2.2%). However, these studies did not use a control group. The comparison was “before–after”, which is affected by the regression to the mean phenomenon as most of these conditions are self-limiting. Thus, Beecher’s studies did not measure the “effect” of placebo. A recent meta-analysis of 114 trials comparing a placebo group with a no-treatment group found no evidence of placebo effect on binary outcomes, and only a rather small effect on pain, thus disproving Beecher’s notion of great and universal placebo-effects.5 This empirical evidence was disregarded by Forder and colleagues. Although there are reasons to use placebo whenever practicable, the bias caused by the absence of a placebo control should not be exaggerated, and the “placebo effect” should also not be misused to support investigators’ own preconceptions.3 Secondly, the trial by Karlowski et al was focused on the effect of vitamin C on the common cold,2 and thus the “placebo effect explanation” in this particularly influential trial is crucial to the biological question. A recent meta-analysis of 55 placebo-controlled trials found that regular vitamin C supplementation had no effect on the incidence of colds in the general population (relative risk [RR], 0.98; 95% CI, 0.95–1.00), but reduced the incidence of colds in people exposed to substantial physical or cold stress (RR, 0.50; 95% CI, 0.38–0.66).6 Also, regular vitamin C intake reduced the duration of colds in adults by 8% (95% CI, 3%–13%) and in children by 13.5% (95% CI, 5%–21%). Although further studies are needed to evaluate the practical significance of these findings, it is evident that the interpretation by Karlowski and colleagues that the effect of vitamin C on the common cold may be explained by the break in the double blind2 is false and should not be reiterated.

Harri Hemilä

Peta M Forder,* Val J Gebski,† Anthony C Keech‡ * Statistician, † Principal Research Fellow, ‡ Deputy Director, NHMRC Clinical Trials Centre, University of Sydney, Locked Bag 77, Camperdown, NSW 1450. enquiryATctc.usyd.edu.au In reply: Allocation concealment refers to ignorance of future treatment assignment before randomisation whereas masking or blinding is most commonly used to refer to the concealment of treatment assignment after randomisation.1 There are two criteria for successful concealment of allocation: (i) physical concealment of the process of random assignment to treatment, and (ii) concealment of any pattern of consecutive assignments. Successful concealment of the process must prevent unauthorised access to randomisation lists, envelopes or algorithms; the best way is to use a centralised or remote service for randomisation, whereby an independent party other than the clinician or investigator accesses a secure sequence list or a secure computer system to generate the next allocation.2,3 Successful concealment of the pattern of random assignments prevents investigators from predicting a future treatment assignment on the basis of pattern recognition of allocations to date. Identifying a pattern of previous allocations can occur in open-label trials, in which all parties are aware of allocated treatments after randomisation, or if the blinding of patients and investigators has been compromised. The likely success of concealing the allocation process can reasonably be judged by its description in most trial reports (usually found in the Methods section). However, it is usually more difficult to assess the likelihood that investigators could have predicted future allocations. Unsuccessful concealment of treatment assignment after randomisation (masking or blinding) should be detailed in the trial report. In circumstances where the blinding has been substantially compromised, exploring the results of treatment separately among participants who were unblinded and those who remained blinded, should be considered, although these are no longer randomised comparisons. In the study by Karlowski et al,4 the placebo did not match the active treatment in taste, which alerted the investigators to the likely occurrence of significant unblinding within the study. To their credit, the investigators sought to quantify the extent of unblinding by means of a questionnaire at study close-out, and reported their findings by results of these responses. The particular grouping of responses, however, has been the subject of some discussion,5,6 and while the interpretation of a possible placebo effect has been challenged, it has not necessarily been disproven. (The absence of a placebo effect could be proven only if information concerning perceived benefits of vitamin C related more to cold frequency than cold symptoms. Biologically, it is far more plausible for a placebo effect to result in fewer cold symptoms reported than fewer colds reported.) This trial highlights the impact of compromised blinding in the reporting of trial results, emphasising the importance of maintaining adequate blinding for reliable and unbiased trial results. Good quality reporting of trials, in accordance with the CONSORT statement,7 includes describing the processes in enough detail to assure readers that any pattern of randomisation is not predictable. Authors should report issues relating to allocation concealment, blinding (where appropriate) and randomisation sufficiently to convey the message that these essential trial principles were successfully achieved.8

Peta M Forder · Val J Gebski · Anthony C Keech

Trial registration, transparency and less reliance on industry trials are essential Over the past 20 years, politicians, hospital administrators and university deans have encouraged academic researchers to increase their participation in projects sponsored by the pharmaceutical industry, and the industry’s share of biomedical research has increased dramatically in that time (from 32% to 62% in the United States).1 Increasingly, the wisdom of this development has been challenged. It would be even better if testing drugs in patients was a public enterprise . . . The research agenda predominantly serves the interests of industry rather than those of patients. Surveys have shown that manipulation of clinical trials — whereby, if the results are published at all, the control treatment is disadvantaged by design, analysis, or interpretation2-5 — is common. Even when the results for the active and control therapies are no different, industry-sponsored trials come to a positive conclusion in favour of the sponsor’s drug five times more often than do not-for-profit-sponsored trials.4 This sponsor bias can have serious consequences. A meta-analysis supported by Merck concluded that there was no increased risk of arterial thrombosis with the company’s cyclo-oxygenase-2 (COX-2) inhibitor, rofecoxib.6 However, another meta-analysis, not sponsored by industry, showed an increased risk, which was apparent in publications available to the authors of the industry-sponsored meta-analysis 4 years before the drug was withdrawn because of thromboses.7 Such down-playing of harms in published papers has often required the collaboration, or acquiescence, of academic clinical researchers. It is likely that the widespread use of COX-2 inhibitors has caused thousands of premature deaths. An article by Henry and colleagues in this issue of the journal (page 557) reports important breaches in research integrity in industry-sponsored research, based on the experience of medical specialists in Australia.8 There are several reasons why the prevalence of the problems probably represents only the tip of the iceberg. Firstly, the authors note that their findings are limited by reliance on self-report, and only 39% responded. Secondly, while only about 9% of respondents reported one or more episodes of potentially serious research misconduct, the authors note that this is equivalent to 21% of those who had an active research relationship with industry. Thirdly, the authors did not consider protocol changes to be serious research misdemeanours. They need not be, but we found that at least one primary outcome was changed, introduced, or omitted while research was under way in 51 of 82 trials (62%).5 We think this is a serious problem as, with a median of 27 outcomes per trial,5 one would expect one outcome to become statistically significant by chance, even if the compared treatments were identical. Finally, 2% of respondents in the paper by Henry et al reported changes to study protocols while trials were under way.8 Our study comparing protocols with corresponding publications showed that formal changes submitted to scientific ethics committees are not common, but that informal changes are. We found that 86% of the respondents in a survey of triallists denied the existence of unreported outcomes, despite clear evidence to the contrary — we did not reveal to them until later that we had access to their trial protocols through the scientific ethics committees.5 Research misconduct and bias in intervention research could be markedly reduced if ongoing initiatives to register all trials at their inception, and ensure public access to trial protocols and all data generated by a trial, become successful. The International Committee of Medical Journal Editors have made a very positive and strong move towards this goal. They have agreed that after 1 July, 2005, its member journals, as a condition of considering a trial for publication, will require that it be registered in a public trials registry before patients enter the trial.9 Ethics committees would also have to play a central role to make this happen, and to ensure that commercial considerations will not be allowed to block access to the collected data, whether or not they are formally published. It would be even better, of course, if testing drugs in patients was a public enterprise (whether or not financed by industry) with blinding during data analysis and writing of manuscripts, till everyone involved had approved them.10 This would ensure that commercial influences on trial design, analysis, manuscript preparation and publication would no longer distort our views of the value of drugs and other treatments. It would also ensure that the comparison treatment was relevant, that the outcomes were directly relevant for patients, and that the patient population was relevant (eg, elderly patients in the case of COX-2 inhibitors, who are also those most likely to develop thromboses). A case in point is the publicly sponsored ALLHAT trial, the biggest trial ever performed on hypertension, which showed that the cheapest drug available was also the best.11 It is clear that governments could save money and treat patients better by investing much more in trials and academic trial centres than by relying on industry’s own trials and conclusions. Who would buy a washing machine that is five or 10 times more expensive than other machines just because its manufacturer has compared it with other machines and claims that it is the best? Unfortunately, such absurdities are often seen in health care, and are allowed to happen even in the absence of any direct head-to-head comparisons.

Peter C Gøtzsche MD, DrMedSci

Objectives: To characterise research relationships between medical specialists and the pharmaceutical industry in Australia.Design and setting: Questionnaire survey of medical specialists listed in the Medical Directory of Australia and believed to be in active practice, conducted in 2002 and 2003.Main outcome measures: Details of medical specialists’ involvement in pharmaceutical industry-sponsored research, and reports of potentially undesirable research outcomes.Results: Of 2120 specialists approached, 823 (39%) responded. Participation in pharmaceutical industry-sponsored research was more commonly reported by those in salaried practice (49%) than those in private practice (33%); P < 0.001. 216 reported that industry had made initial contact, compared with 117 who had initiated contact with industry. 14.0% of respondents reported premature termination of industry-sponsored trials, which they considered appropriate when in response to concerns about adverse drug effects. 12.3% of respondents reported that industry staff had written first drafts of reports, which they viewed as an acceptable practice for “internal” documents only. Of greatest concern to respondents were instances of delayed publication or non-publication of key negative findings (reported by 6.7% and 5.1% of respondents, respectively), and concealment of results (2.2%). Overall, 71 respondents (8.6%) had experienced at least one event that could represent breaches of research integrity.Conclusions: These data indicate a high level of engagement in research between the pharmaceutical industry and medical specialists, including those in private practice. Examples of possibly serious research misconduct were reported by 8.6% of respondents, equivalent to 21% of those with an active research relationship with industry.

David A Henry MB ChB, MRCP, FRCP · Suzanne R Hill PhD, GradDipEpi, FAFPHM · Evan Doran BA, PhD · David A Newby BPharm, PhD · Kim M Henderson BNurs, GradDip(HealthSocSci) · Jane Maguire BA, BNurs(Hon) · Barrie J Stokes BSc, MMath · Ian H Kerridge MPhil, FRCPA, FRACP · Paul M McNeill MA, LLB, PhD · Richard O Day MD, FRACP · Graham J Macdonald MD, FRACP, FRCP

Edwin P Kirk,* Annette Hattam,† Anne Turner‡ * Co-ordinator of Advanced Training, † Chair, Specialist Advisory Committee in Clinical Genetics, Royal Australasian College of Physicians; and Geneticists, Department of Medical Genetics, Sydney Children’s Hospital, High Street, Randwick, NSW 2031; ‡ Chairperson, Board of Censors in Genetic Counselling, Human Genetics Society of Australasia. kirkedATsesahs.nsw.gov.au To the Editor: Genetic risk estimation is a key element of the practice of clinical geneticists and genetic counsellors. Given this, it was with some concern that we read the findings of Bonke and colleagues regarding the performance of (mainly European) geneticists and counsellors in the application of Bayesian analysis to risk estimation.1 Bayesian analysis is taught as part of Australasian training in both clinical genetics and genetic counselling, and has been for as long as there have been formal programs. Thus, most Australian geneticists and counsellors should be familiar with the application of Bayes’ theorem to risk estimation. In actual clinical practice, it is rare to need to perform this type of analysis. This is partly because of the rapid progress in molecular genetic testing, which often obviates the need for such calculations, and partly because situations in which Bayesian analysis is clinically helpful are uncommon. Pedigrees like those in the study by Bonke et al do not come along often; when they do, the modification of prior risk by Bayesian analysis is not often important. For example, modification of a risk from 50% to 33% or from 25% to 17% (as in two of the examples used by Bonke et al) is unlikely to alter decision-making for the families involved. Specifically, as these examples all involve testing for Huntington’s disease, in which molecular analysis is usually quite straightforward, we would expect very few individuals would decide whether to proceed with testing based on being given information about modification of risk expressed this way. Moreover, when you are not performing this type of calculation regularly, it is time-consuming to do. It seems possible that many of those who completed the questionnaire would have taken greater care, and achieved greater accuracy, if faced by a real clinical situation. Nonetheless, for those of us who are involved in training clinical geneticists and genetic counsellors, the article is a useful reminder of the importance of this skill, and we will communicate with supervisors to reinforce the importance of teaching Bayesian analysis to our trainees.

Edwin P Kirk · Annette Hattam · Anne Turner

In reply: Geneticists and counsellors must be able to calculate risks according to professional standards, regardless of whether modified risks lead to decision changes. Does training in genetic risk calculation help? Only 21% of our respondents who had had such training recently (< 3 years ago) estimated all target risks correctly. In response to Kirk et al, calculating conditional risks need not be time-consuming in scenarios similar to our target pedigrees,1 and is often helpful when at-risk (grand)parents do not wish to be tested but their offspring do. Given n children at 25% prior risk tested negative and no other (grand)children tested, the conditional risk for at-risk individuals in generation g (with g = 0 at 50% prior risk, g = 1 at 25% prior risk, etc) is 1/[2g(2n+1)]. Thus, in target #4 (n = 1), the father’s risk (g = 0) equals 1/[20(21+1)] = 0.33. In target #9 (n = 2), the unborn’s risk (g = 2) equals 1/[22(22+1)] = 0.05. Similar formulas for more complicated scenarios are available upon request. In calculating risks, however, care must be taken that the pedigrees and target individuals are comparable to our scenarios. In target #7, for instance, the risk for the untested aunt does not increase simply because of the decreased risk for her brother (gambler’s fallacy).2

Benno Bonke · Aad Tibben · Dick Lindhout · Angus J Clarke · Theo Stijnen

Aim: To estimate national rates of induced abortion in Australia from 1985 to 2003, using Medicare claim statistics for private patients and hospital morbidity statistics for public patients.Design and setting: Estimates were based on Australian and South Australian data collections relating to abortions. SA hospital morbidity statistics were compared with SA statutory notifications of abortions to estimate the accuracy of these collections. Medicare statistics on abortion procedures performed on private patients in South Australia were then compared with hospital morbidity statistics for private patients. National statistics on abortion derived from Medicare and hospital morbidity statistics were adjusted for inaccuracies found in these sources.Main outcome measures: Numbers of induced abortions in Australia for each year from 1985 to 2003; abortion rates per 1000 women aged 15–44 years.Results: Abortion numbers based on Medicare claims by private patients overestimated by 18.7% the number of abortions derived from statutory notifications in South Australia during the period 1988–89 to 1999–00. Hospital morbidity data using principal diagnosis codes relating to medical abortion overestimated statutory notifications by 2.3% (mainly because of readmissions). National statistics were adjusted for these overestimations and for the estimated 14.1% of private patients who would not have submitted Medicare claims (based on surveys of private-clinic patients in New South Wales and Victoria). The estimated Australian abortion rate increased from 17.9 per 1000 women aged 15–44 in 1985 to a peak of 21.9/1000 in 1995, then declined to 19.7/1000 in 2003 (estimated number of abortions, 84 460).Conclusion: There are no data currently available for deriving accurate numbers of induced abortions in Australia. Suggestions are made for collection of national statistics.

Annabelle Chan MB BS, FAFPHM · Leonie C Sage RN, RM

Australia has so far been spared serious mishaps in health research, but rising pressures on researchers, deemed to have contributed to two deaths of research participants in the United States, clearly also exist in Australia. Health research investment in our institutions is large and represents an often overlooked area of risk by boards of management. Research governance (the framework through which institutions are ultimately accountable for the scientific quality, ethical acceptability and safety of research conducted in the institutions) has not received sufficient attention. An adequate governance framework requires institutions to have policies and procedures in place to meet national ethical, legal and research practice standards. We suggest that many institutions presently do not have such frameworks in place and inappropriately rely too heavily on human research ethics committees. To ensure ongoing adequate protection of research participants, we recommend some simple improvements for research governance and suggest ways by which institutions can demonstrate adherence to agreed national standards.

Michael K Walsh MB BS, MPA, FRACMA · John J McNeil MB BS, PhD, FRACP · Kerry J Breen MB BS, MD, FRACP

Objective: To examine trends in adverse drug reactions (ADRs) in people aged 60 years or over causing admission to or an extended stay in Western Australian hospitals between 1981 and 2002.Design and setting: Secondary data analysis of case series.Patients: 43 380 patients admitted to WA public and private hospitals with an (International Classification of Diseases) ICD external cause code for an ADR, identified by the population-based WA Hospital Morbidity Data System.Main outcome measures: Age-specific, age-standardised and drug-specific rates of ADR-related hospital stays.Results: The age-standardised rate of ADR-related hospital stays increased from 2.5 per 1000 person-years (py) in 1981 to 12.9 per 1000 py in 2002. The largest increases occurred in those aged 80 + years (tenfold in men and sevenfold in women). The most common drug group involved was cardiovascular agents (17.5%), while anticoagulants (7.5%), cytotoxics (7.4%) and antirheumatics (6.8%) were the more specific drug classes most often implicated. ADRs from the last three classes of drugs were still rising at the end of the study, whereas ADRs from corticosteroids and antihypertensives peaked in 1996 and from opioids in 2000.Conclusions: Increases in hospital admissions or extended lengths of stay due to ADRs in WA have continued despite programs to promote rational and safer use of medicines. The sharp increase in ADRs from anticoagulants warrants attention to revised clinical guidelines.

Christel L Burgess BHlthSc(Hons) · C D’Arcy J Holman MB BS, MPH, PhD · Anthony G Satti BEd

Objective: To study the impact of various risk factors on survival time in a cohort of elderly Australians.Design, setting and participants: A longitudinal, prospective cohort study conducted in Dubbo, NSW. Participants were men and women aged 60 years or over living in the community, first assessed in 1988–1989 and followed for 15 years.Main outcome measures: Mortality rates; risk factors; survival times.Results: There were 668 deaths in 1233 men (54%) and 625 deaths in 1572 women (40%). Coronary heart disease was the major cause of death, rates being higher in men than women until age group 80+ years; stroke death rates were similar in both sexes; cancer and respiratory death rates were higher in men than women across all ages. In a proportional hazards model, the independent predictors of mortality were cigarette smoking, diabetes, very high blood pressure (BP), impaired peak expiratory flow (PEF), physical disability, and zero intake of alcohol. Over 15 years, the average reductions in survival time associated with various risk factors, in men and women respectively, were smoking, 22 and 15 months; diabetes, 18 and 18 months; very high BP, 16 and 9 months; impaired PEF, 14 and 17 months; physical disability, 16 and 12 months; zero alcohol intake, 9 and 5 months. Combinations of selected risk factors were associated with a multiplier effect.Conclusion: The reduction in survival time in elderly citizens demonstrated in the presence of smoking, diabetes and hypertension highlights a potential benefit to healthy ageing to be gained from prevention and intervention.

Leon A Simons MD, FRACP · Judith Simons MACS · John McCallum DPhil · Yechiel Friedlander PhD

Raoul A Walsh,* Judith Lumley† * Senior Research Academic, Centre for Health Research and Psycho-oncology, The Cancer Council NSW/University of Newcastle, Locked Bag 10, Wallsend, NSW 2287. † Director, Mother and Child Health Research, La Trobe University, Melbourne, VIC. Raoul. WalshATnewcastle.edu.au To the Editor: Problems with interpreting odds ratios reported in meta-analyses of smoking-cessation interventions have recently been highlighted.1 Ford and Dobson2 have erred in a different way when applying the findings of the Cochrane review on smoking cessation interventions in pregnancy3 to calculate the public health benefits of delivering such interventions to all pregnant women in Australia. When all methodologically acceptable randomised controlled trials were considered, the Cochrane review did find the prevalence of smoking at end-of-pregnancy was 6% lower in intervention than control groups.3 However, this does not equate to a 6% reduction in the population prevalence of smoking among pregnant women, as Ford and Dobson assume. A mean between-group difference reported in a meta-analysis is not equivalent to a difference of exactly the same magnitude in a population prevalence of a risk factor unless 100% of the population exhibit that risk factor. Clearly, as Ford and Dobson have reported, this is not the case with smoking in pregnancy, where they correctly note that about 20% of pregnant women report current smoking at their first antenatal visit.2 Therefore, smoking-cessation interventions would not reduce the prevalence of smoking by 6% from 20% to 14%. The expected reduction can be calculated as follows: expected reduction in prevalence of smoking in pregnant women = current smoking prevalence in pregnant women (20%) × between-group difference in smoking prevalence (0.06) = 1.2%. This calculation rests on two assumptions: namely, that all pregnant women in Australia currently receive usual smoking-cessation care equivalent to that of control group conditions in the Cochrane review3 and that, in the short term, antenatal care can be transformed to the point where all future pregnant women receive smoking-cessation care equivalent to that received by those in intervention groups in the Cochrane review. Therefore, it is obvious that the expected smoking prevalence of 18.8% (20% minus 1.2%) is considerably higher than the 14% calculated by Ford and Dobson.2 Unfortunately, this means the rates of reduced infant deaths, hospital separations and costs to the healthcare system estimated by Ford and Dobson have also been overstated. In summary, the gains to be expected by clinical interventions with pregnant smokers are modest. Furthermore, past evaluations of media campaigns directed specifically at pregnant women have not shown significant positive effects.4 This reinforces the importance of tobacco-control strategies which target the whole population in addition to those which target pregnant women.5

Raoul A Walsh · Judith Lumley

Jessica H Ford,* Annette J Dobson† * Research Assistant, † Professor of Biostatistics, School of Population Health, University of Queensland, Herston Road, Herston, Brisbane, QLD 4006. J. FordATsph.uq.edu.au In reply: We thank Walsh and Lumley for correcting the error in our letter. The 6% reduction in smoking during pregnancy referred to an absolute difference in prevalence of continued smoking in late pregnancy among women who smoked early in pregnancy, from 91% in the control groups to 85% in the treatment groups.1 We incorrectly hypothesised a reduction from 20% to 14% in prevalence of any smoking during pregnancy. In fact, there was a decline in smoking during pregnancy, from 22% in 1994 to 17% in 2001 in New South Wales.2 These figures illustrate well the final point that Walsh and Lumley make: whole-of-population approaches to smoking reduction can yield much greater benefits (a 5% reduction in 7 years in NSW) than high-risk approaches (from our data, the 1.2% calculated by Walsh and Lumley). Our estimates of the adverse effects of smoking in pregnancy are, at present, correct. Although we unfortunately overstated the possible reductions resulting from interventions targeted only at pregnant women, such reductions are plausible for whole-of-population approaches.3

Jessica H Ford · Annette J Dobson

Aim: To ascertain the incidence of autism spectrum disorders in Australian children.Setting: New South Wales (NSW) and Western Australia (WA), July 1999 to December 2000.Design: Data were obtained for WA from a prospective register and for NSW by active surveillance.Main outcome measures: Newly recognised cases of autism spectrum disorders (defined as autistic disorder, Asperger disorder and pervasive developmental disorder not otherwise specified [PDD-NOS]) in children aged 0–14 years; incidence was estimated in 5-year age bands (0–4 years, 5–9 years, 10–14 years).Results: In WA, 252 children aged 0–14 years were identified with autism spectrum disorder (169 with autistic disorder and 83 with Asperger disorder or PDD-NOS). Comparable figures in NSW were 532, 400 and 132, respectively. Most children were recognised with autistic disorder before school age (median age, 4 years in WA and 3 years in NSW). Incidence of autistic disorder in the 0–4-years age group was 5.5 per 10 000 in WA (95% CI, 4.5–6.7) and 4.3 per 10 000 in NSW (95% CI, 3.8–4.8). Incidence was lower in older age groups. The ratio of all autism spectrum disorders to autistic disorder alone was 1.5:1 in WA and 1.3:1 in NSW, and rose with age (1.8:1 and 2.9:1 in 10–14-year-olds in WA and NSW, respectively).Conclusions: These are the first reported incidence rates for autism for a large Australian population and are similar to rates reported from the United Kingdom. Ongoing information gathering in WA and repeat active surveillance in NSW will help to monitor any future changes.

Katrina Williams PhD, FRACP, FAFPHM · Megan Helmer MHlthSc(CDM) · Craig M Mellis MPH, MD, FRACP · Marshall Tuck MPH · Emma J Glasson PhD · Carol I Bower MSc, PhD, FAFPHM · John Wray FRACP

Objective: To compare attitudes of Australian physicians and paediatricians about treatment and randomised controlled trial (RCT) participation.Design and participants: A cross-sectional survey using the validated “Physician Orientation Profile” (POP), with 250 physicians and 250 paediatricians surveyed.Outcome measures: Five indices — primary allegiance, decision making under uncertainty, professional activities, perceived rewards, and peer-group influence — with scores for each participant ranging along a continuum from clinician-oriented to research-oriented and expressed as a number between 0 and 1.Results: Overall response rate was 60%, with 135 physicians (54%) and 165 paediatricians (66%) responding. Paediatricians and physicians were similar in their attitudes to RCT participation, being generally clinician-oriented rather than research-oriented and less inclined to participate in RCTs when there is uncertainty about the best treatment. Most assign limited time to research, with 26.9% not currently involved in research and 31.5% having no experience of RCT participation. Doctors perceive few rewards and little peer-group influence regarding trial participation. Independent predictors of favourable attitudes to trial participation (based on POP scores) were the presence of allocated research time (0.37 for no allocated research time v 0.61 for > 70% research time; P < 0.0001), previous experience enrolling a patient in an RCT (0.40 for no experience v 0.46 for experience; P < 0.0001), and articles published in the past 12 months (0.40 for no publications v 0.55 for > 3 publications; P < 0.0001).Conclusions: This study highlights the minor importance of research for most Australian physicians. Research plays only a small role in their professional activities, and the importance of research participation is not recognised. They are clinician-oriented in their attitudes to RCT participation. To encourage greater involvement in trials among physicians in Australia, clinical research needs to be restructured in a primarily clinically oriented setting with dedicated research time.

Patrina H Y Caldwell FRACP, PhD · Jonathan C Craig FRACP, PhD · Phyllis N Butow MClinPsych, PhD

QuestionCan a regimen of chewing sucrose-free gum after meals reduce the incidence of caries and remineralise white spot lesions (demineralised and non-cavitated incipient caries) in a population with a moderate incidence of caries? Trial details Design: A cluster-randomised controlled trial with two arms. Setting: Elementary schools in Budapest, Hungary, where water was not fluoridated at the time of the study. Participants: 583 schoolchildren aged 8–13 years (mean age, 9.6 years). Participants and their parents or guardians were required to sign an informed consent form. Non-participation rates and profiles were not reported, and inclusion and exclusion criteria were not specified. Interventions: The intervention group chewed sucrose-free gum (65% polyols [sorbitol and mannitol], 30% gum base and 5% sweeteners and flavours) for 20 minutes after meals, three times a day; the control group did not chew gum. Two meals a day were available at the schools, facilitating supervision of gum chewing. Other chewing sessions were unsupervised. After baseline clinical examination, classes within grade levels were randomly assigned to either arm, provided that each grade level had more than one class with sufficient participants available. No significant differences in baseline caries scores were detected between the intervention and control groups. No modifications were made to the oral hygiene and dietary practices of participants. Main outcome measures: Participants were examined at 1 and 2 years by a single blinded examiner, using a mouth mirror, explorer and transillumination to aid diagnosis of interproximal caries. Drying of teeth and radiographs were not used. Clinical examination results were expressed as World Health Organization (WHO) DMFS (decayed, missing and filled surfaces) scores or Radicke scores. WHO DMFS scores include a category for incipient carious lesions, and are commonly used caries experience indices, quantifying decayed, missing and filled surfaces. Main results: 1-year and 2-year scores for DMFS increment were adjusted for by baseline DMFS scores. Using the Radicke DMFS scores, reductions in caries increment for the intervention group were in the order of 43.6% (P = 0.008) and 38.7% (P = 0.018) at 1 and 2 years, respectively. Using the WHO DMFS scores (inclusive of incipient lesions), reductions in caries increment for the intervention group were in the order of 41.7% (P = 0.028) and 33.1% (P = 0.008) at 1 and 2 years, respectively. Conclusions: The authors concluded that chewing sucrose-free gum after meals provided a positive anti-caries effect. CommentaryRationale for the trialTo confirm previous trials reporting positive anti-caries effects of sucrose-free gum chewing.1-5 Whereas most previous trials were conducted in populations with a high incidence of caries, the authors sought to investigate within an industrialised population with moderate caries incidence. Trial methodsAs no intervention was elected for the control group, participant blinding was not feasible. Thus, the authors did not offer alternative explanations for the positive result. The intervention may have initiated different preventive oral hygiene and dietary practices between groups. Also, the intervention group may have been less likely to seek confectionery, and hence a less cariogenic diet, compared with the control group. Participant flow was poorly reported, obscuring potential sources of bias. Follow-up was excellent, with 93.8% presenting for 2-year clinical examination. However, this follow-up rate was not broken down between intervention and control groups. It is feasible that this rate may have been lower in the more procedurally demanding intervention group, and those not presenting for follow-up may represent participants with less concern for their oral health. Reporting of withdrawal after randomisation (of particular interest to the intervention group) was also poor. Mechanisms for capturing adverse events were not described. No adverse events were reported, except for one that was not related to the chewing gum, but resulted in withdrawal. There is concern that adverse events not related to the chewing gum were not adequately monitored. Compliance, especially for out-of-school chewing, is a challenge in a trial such as this. School chewing compliance was reported as unproblematic, but the method of monitoring was not described. Out-of-school chewing compliance was assessed by gum wrapper return (93% of students returned more than 90% of wrappers). This does not accurately reflect if gum was chewed and by whom. The authors recognised that gum chewing could not be accurately assessed in the control group. However, prohibition of gum chewing in schools was described. New informationThis study suggests a positive anti-caries effect of chewing sucrose-free chewing gum after meals within an industrialised population with moderate caries incidence. To confirm such an effect, the role of bias would require greater attention. Implications for clinical practiceThe authors advise that sucrose-free gum-chewing be considered on an individual and organisational level. From the perspective of a cost–benefit analysis, this is premature. The gum-chewing regimen described is expensive and needs to be considered against other preventive measures, such as fluoride gels and mouth rinses, before the authors’ recommendations can be embraced. The evidence for the superior efficacy of chewing gum sweetened with xylitol over that sweetened with sorbitol is not unanimous.3-5 Budapest may benefit more from fluoridation of its water supply.

Claudine E Tsao BDSc · Michael V Morgan BDSc, MDSc, PhD