- Email: [email protected]
Update on effects of screening mammography
CORRESPONDENCE
comorbidity in these ageing women may lead to difficult decisions in defining the underlying cause of death.5 Olsen and Gøtzsche showed there was no change in cancer mortality. Prestated hypotheses on competing cancer diagnoses may rule out simple misclassification. These data are available in the database used by Nyström and colleagues. Screening trials support individual and public decisions. The absolute risks and risk reductions must be mentioned explicitly. The absolute risk reduction, calculated from Nyström and colleagues’ data, is seven per 100 000 person-years. After 16 years of followup, 135 breast-cancer deaths were saved among nearly 130 000 women. Whatever the effect of breast-cancer screening, in low-risk populations it is bound to be small. Well-informed women should decide whether one per 1000 winners makes a good bet. Luc Bonneux Julius Centre for Health Sciences and Primary Care, HP D 01.335, PB 85500, 3508 GA Utrecht, Netherlands (e-mail: [email protected]) 1
2
3
4
5
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Olsen O, Gøtzsche PG. Cochrane review on screening for breast cancer with mammography. Lancet 2001; 358: 1340–42. Tabár L, Vitak B, Chen H-H, et al. The Swedish Two-County trial twenty years later: updated mortality results and new insights from long-term follow-up. Radiol Clin North Am 2000; 38: 625–51. Black WC, Haggstrom DA, Welch H. All cause mortality in randomized trials of cancer screening. J Natl Cancer Inst 2002; 94: 167–73. Coebergh J, Janssen-Heijnen M, Post P, Razenberg P. Serious co-morbidity among unselected cancer patients newly diagnosed in the southeastern part of The Netherlands in 1993-1996. J Clin Epidemiol 1999; 52: 1131–36.
Sir—Lennarth Nyström and colleagues’ updated overview1 does not resolve the fundamental issue of whether screening decreases mortality. They report a 2% (non-significant) reduction in total mortality and state they would have expected a 2·3% reduction. However, the breast-cancer mortality is 27% (not 17% as mistakenly printed), and, weighted by size of invited group, the expected reduction is only 0·9% (calculated as [13·2%⫻9%⫻49 044+7·2%⫻12%⫻ 47 354+3·2%⫻27%⫻27 983–2·1%⫻ 1 2 % ⫻5 3 6 9 ] / [ 4 9 0 4 4 + 4 7 3 5 4 + 27 983+ 5369]). Their inflated estimate is driven by the Östergötland part of the TwoCounty trial,2 which contributed about
338
half of the deaths (relative risk for total mortality 0·98). Socioeconomic factors are strong mortality predictors and could easily explain a 2% reduction in total mortality, but such data for the Östergötland trial remain unpublished. Nyström and colleagues report that pretrial breast-cancer incidence and breast-cancer mortality were similar in the invited and control groups, but the power of their test was very low, and cannot compare socioeconomic factors. The overview is not credible without publication of the baseline data. Furthermore, the number of randomised women is larger than in the 1993 overview,3 although both overviews were based on exact age at randomisation and the age range is the same. The unadjusted and age-adjusted estimates for total mortality are, surprisingly, the same, with relative risk 0·98. In the 1993 Swedish overview, these were 1·00 and 1·06 (95% CI 1·04–1·08), respectively.3 The number of person-years of followup was 2·6 million in 1993 and 3·5 million in 2002. The Kopparberg part of the Two-County trial was not available for Nyström and colleagues’ overview, but the extended data for the Malmö trial (reference 4 in the report) were. How can these changes result in such a large difference? Despite its sound methods, Nyström and colleagues exclude the Canadian trial4 because mammography and breast self-examination or physical examination are combined and because it is not population based. However, invited women in the TwoCounty trial were encouraged to do self-examination, and whether or not a trial is population based is not a relevant exclusion criterion. The investigators take no account of clustering because methods for overview of trials with different methods of randomisation are inadequate. However, individual trials can be compared and the estimates combined. Nyström and colleagues seem to have analysed the trials as if they were cohort studies, but do not explain how they dealt with those that are not fully randomised. There is a notable unexplained discrepancy between the current numbers and those in the final report of the Stockholm trial and those in the 1993 overview, in which the number of randomised women falls in the screening group, but increases in the control group.3 However, the numbers should be the same. The Göteborg trial (their references 9 and 10) is also problematic. Nyström and colleagues
report that the randomisation ratio was 1·6 (control vs invited) in the agegroup 50–59 years, but birth-year cohorts were randomised successively with the ratio adjusted according to the capacity of the screening unit (N Bjurstam, personal communication). These ratios were most extreme for the oldest and the youngest birth-year cohorts. Since breast-cancer mortality increases with age, a bias arises in favour of screening that can be removed only by comparing the results within each birth-year cohort before they are lumped together. No such procedure is described in any trial report or overview. For the extended Malmö data, women were supposed to be included at age 45 years, yet 6780 women aged 40–44 were included. The number of randomised women in the original Malmö trial is also larger than Nyström and colleagues report, and the numbers differ substantially in the invited and control-group birth-year cohorts. Computer randomisation, however, means these numbers should not differ. Trial times were calculated as date of randomisation until the date the control group had completed the first round of screening. The treatment contrast, however, should be calculated as the difference between the dates screening started in the invited and control groups. Since screening of the control group was completed later than planned, there is bias in favour of screening, especially for the Göteborg trial.5 Giving the numbers of breast-cancer deaths for each trial according to the follow-up model would allow other researchers to do their own analyses. The assessment of cause of death might have been biased in favour of screening in the Two-County trial. There are other important unresolved issues. A meta-analysis from independent researchers is therefore crucial, based on the raw data from all the screening trials, using total mortality as the primary outcome. Peter C Gøtzsche Nordic Cochrane Centre, Rigshospitalet Dept 7112, DK-2100 Copenhagen, Denmark (e-mail: [email protected])
1
2
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist L. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Tabár L, Fagerberg CJ, Gad A, et al. Reduction in mortality from breast cancer after mass screening with mammography. Randomised trial from the Breast Cancer Screening Working Group of the Swedish
THE LANCET • Vol 360 • July 27, 2002 • www.thelancet.com
For personal use. Only reproduce with permission from The Lancet Publishing Group.
CORRESPONDENCE
3
4
5
National Board of Health and Welfare. Lancet 1985; 1: 829–32. Nyström L, Rutqvist LE, Wall S, et al. Breast cancer screening with mammography: overview of Swedish randomised trials. Lancet 1993; 341: 973–78. Miller AB, Baines CJ, To T, Wall C. Canadian National Breast Screening Study, 2: breast cancer detection and death rates among women aged 50 to 59 years. CMAJ 1992; 147: 1477–88. Berry DA. Benefits and risks of screening mammography for women in their forties: a statistical appraisal. J Natl Cancer Inst 1998; 90: 1431–39.
Sir—The updated overview of Lennarth Nyström and colleagues1 addresses many issues raised by Gøtzsche and However, the following Olsen.2 information could provide further reassurance about the validity of the Swedish findings. First, the number of women excluded because of a diagnosis of breast cancer before randomisation in the invited and control groups should have been presented. Although Nyström and colleagues had relied on the data in the Swedish Cancer Registry as the basis of exclusion, if being in the invited group led to more thorough attention that increased the chance of a previous diagnosis being ascertained and registered, there could still be a bias. Such an effect, according to Gøtzsche and Olsen, seemed to have been a problem in the New York trial.3 If similar proportions were excluded in each group in each of the Swedish trials, bias is unlikely. Second, details of the distribution of individual baseline characteristics other than age would have been useful. The availability of such information might be limited if control women were not interviewed at the start of the study. However, certain relevant characteristics may be relatively stable. One example is socioeconomic status, which has prognostic importance in many populations, including the UK.4 K K Cheng Department of Public Health and Epidemiology, University of Birmingham, Public Health Building, Edgbaston, Birmingham B15 2TT, UK (e-mail: [email protected]) 1
2
3
4
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Gøtzsche PC, Olsen O. Is screening for breast cancer with mammography justifiable? Lancet 2000; 355: 129–34. Shapiro S, Venet W, Strax P, Venet L, eds. Periodic screening for breast cancer. Baltimore: Johns Hopkins University Press, 1998. Coleman MP, Babb P, Damiecki P, et al. Cancer survival trends in England and Wales, 1971-1995: deprivation and NHS Region. London: Stationery Office, 1999.
Sir—Lennarth Nyström and colleagues1 present a significant 21% risk reduction in breast-cancer mortality, based on the Swedish randomised controlled mammography trials. The corresponding absolute risk of death from breast cancer in the control groups was 584 (0·0050%) per 117 260 women, and in the intervention groups 511 (0·0039%) per 129 750 women. Based on these numbers, 960 women need to be screened to save one life in 6·5 years. In the age-group with the most favourable results, 55–69 years, the corresponding numbers were 305 (0·0065%) per 46 989 and 240 (0·0045%) per 52 877 women in the control and intervention groups, respectively. 512 women need to be screened to save one life in 6·5 years. To decide whether these findings warrant mammography screening as part of health services financed by the state is a normative question, not a medical one. In democratic societies, people prefer to choose which health services to use. Services not provided by official authorities can be bought on the free market. Under these conditions, the concept of screening is not applicable, as far as reliable criteria for the assessment of screening programmes are concerned. People at greater risk of disease are inclined not to attend, and those who are not offered screening (eg, younger age-groups), buy it if they think they need it. Only if a screening procedure is simple, cheap given the consequences of not providing it, and possible to apply on almost all of the defined target population should it be a task for the state. Gelmon and Olivotto, in their accompanying March 16 Commentary,2 rightly urge more timely and cost-effective procedures than mammography. They are wrong, however, to encourage women aged 55–69 to attend screening. Instead, the detection of breast cancer should be based on proper medical assessment in general practice, and referral when necessary. Pål Gulbrandsen HELTEF Centre for Health Services Research, PO Box 55, 1474 Nordbyhagen, Norway (e-mail: [email protected]) 1
4
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Long-term effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Gelmon KA, Olivotto I. The mammography screening debate: time to move on. Lancet 2002; 359: 904–5.
THE LANCET • Vol 360 • July 27, 2002 • www.thelancet.com
Authors’ reply Sir—Laszlo Tabár and colleagues claim that the Östergötland county is currently participating in the overview without the consent of the county’s lead investigator. The trialists of Stockholm and Östergötland, Lars Hellström and Gunnar Fagerberg, retired several years ago and were replaced by Jan Frisell and Bedrich Vitak. Vitak participated in the group initially, then chose to withdraw, but has now announced renewed interest in participating in collaborations. Luc Bonneux notes the differences in the effect of invitation to mammography screening in the Östergötland trial in our overview and in Tabár and colleagues’ follow-up (11 vs 24%). These could be due to different followup times and sources for breast-cancer diagnosis and cause-of-death classification (Swedish Cancer Register vs local endpoint committee). Bonneux also believes that bias may distort the effect of screening. Sticky bias is valid in the prevalence round in the invited group, as seen in the pretrial and trial data for Östergötland (see figure 1 in our report). There was a similar increase in the control group when they were invited to the prevalence round. Sticky bias, however, results only in more conservative estimates. The issue of slippery bias was specifically addressed in our early follow-up of the cause of death pattern through 1989.1 The relative risk of malignant neoplasm in the digestive, respiratory, and urogenital organs, and for leukaemia as underlying cause of death in the invited group compared with the control group was 1·05, 1·02, 0·97, and 1·03, respectively; there was no indication for a slippage towards other cancer sites. Furthermore, during the trial period, patients underwent modern radiotherapy, which has minimal or no risk of cardiac complication. Bonneux finds the effect of the intervention small without considering that in the Swedish trials women were, over an average period of 6·5 years, invited to an average of three rounds. We do not agree. Peter Gøtzsche repeats the criticism from his and Olsen’s previous publications.2,3 Space limitations and the fact that each trial is preparing a separate publication make it look like we focused on only a few questions. Gøtzsche and K K Cheng ask for pretrial background characteristics. No pretrial data were collected in the Swedish trials. We presented pretrial breast-cancer morbidity and mortality
339
For personal use. Only reproduce with permission from The Lancet Publishing Group.
comorbidity in these ageing women may lead to difficult decisions in defining the underlying cause of death.5 Olsen and Gøtzsche showed there was no change in cancer mortality. Prestated hypotheses on competing cancer diagnoses may rule out simple misclassification. These data are available in the database used by Nyström and colleagues. Screening trials support individual and public decisions. The absolute risks and risk reductions must be mentioned explicitly. The absolute risk reduction, calculated from Nyström and colleagues’ data, is seven per 100 000 person-years. After 16 years of followup, 135 breast-cancer deaths were saved among nearly 130 000 women. Whatever the effect of breast-cancer screening, in low-risk populations it is bound to be small. Well-informed women should decide whether one per 1000 winners makes a good bet. Luc Bonneux Julius Centre for Health Sciences and Primary Care, HP D 01.335, PB 85500, 3508 GA Utrecht, Netherlands (e-mail: [email protected]) 1
2
3
4
5
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Olsen O, Gøtzsche PG. Cochrane review on screening for breast cancer with mammography. Lancet 2001; 358: 1340–42. Tabár L, Vitak B, Chen H-H, et al. The Swedish Two-County trial twenty years later: updated mortality results and new insights from long-term follow-up. Radiol Clin North Am 2000; 38: 625–51. Black WC, Haggstrom DA, Welch H. All cause mortality in randomized trials of cancer screening. J Natl Cancer Inst 2002; 94: 167–73. Coebergh J, Janssen-Heijnen M, Post P, Razenberg P. Serious co-morbidity among unselected cancer patients newly diagnosed in the southeastern part of The Netherlands in 1993-1996. J Clin Epidemiol 1999; 52: 1131–36.
Sir—Lennarth Nyström and colleagues’ updated overview1 does not resolve the fundamental issue of whether screening decreases mortality. They report a 2% (non-significant) reduction in total mortality and state they would have expected a 2·3% reduction. However, the breast-cancer mortality is 27% (not 17% as mistakenly printed), and, weighted by size of invited group, the expected reduction is only 0·9% (calculated as [13·2%⫻9%⫻49 044+7·2%⫻12%⫻ 47 354+3·2%⫻27%⫻27 983–2·1%⫻ 1 2 % ⫻5 3 6 9 ] / [ 4 9 0 4 4 + 4 7 3 5 4 + 27 983+ 5369]). Their inflated estimate is driven by the Östergötland part of the TwoCounty trial,2 which contributed about
338
half of the deaths (relative risk for total mortality 0·98). Socioeconomic factors are strong mortality predictors and could easily explain a 2% reduction in total mortality, but such data for the Östergötland trial remain unpublished. Nyström and colleagues report that pretrial breast-cancer incidence and breast-cancer mortality were similar in the invited and control groups, but the power of their test was very low, and cannot compare socioeconomic factors. The overview is not credible without publication of the baseline data. Furthermore, the number of randomised women is larger than in the 1993 overview,3 although both overviews were based on exact age at randomisation and the age range is the same. The unadjusted and age-adjusted estimates for total mortality are, surprisingly, the same, with relative risk 0·98. In the 1993 Swedish overview, these were 1·00 and 1·06 (95% CI 1·04–1·08), respectively.3 The number of person-years of followup was 2·6 million in 1993 and 3·5 million in 2002. The Kopparberg part of the Two-County trial was not available for Nyström and colleagues’ overview, but the extended data for the Malmö trial (reference 4 in the report) were. How can these changes result in such a large difference? Despite its sound methods, Nyström and colleagues exclude the Canadian trial4 because mammography and breast self-examination or physical examination are combined and because it is not population based. However, invited women in the TwoCounty trial were encouraged to do self-examination, and whether or not a trial is population based is not a relevant exclusion criterion. The investigators take no account of clustering because methods for overview of trials with different methods of randomisation are inadequate. However, individual trials can be compared and the estimates combined. Nyström and colleagues seem to have analysed the trials as if they were cohort studies, but do not explain how they dealt with those that are not fully randomised. There is a notable unexplained discrepancy between the current numbers and those in the final report of the Stockholm trial and those in the 1993 overview, in which the number of randomised women falls in the screening group, but increases in the control group.3 However, the numbers should be the same. The Göteborg trial (their references 9 and 10) is also problematic. Nyström and colleagues
report that the randomisation ratio was 1·6 (control vs invited) in the agegroup 50–59 years, but birth-year cohorts were randomised successively with the ratio adjusted according to the capacity of the screening unit (N Bjurstam, personal communication). These ratios were most extreme for the oldest and the youngest birth-year cohorts. Since breast-cancer mortality increases with age, a bias arises in favour of screening that can be removed only by comparing the results within each birth-year cohort before they are lumped together. No such procedure is described in any trial report or overview. For the extended Malmö data, women were supposed to be included at age 45 years, yet 6780 women aged 40–44 were included. The number of randomised women in the original Malmö trial is also larger than Nyström and colleagues report, and the numbers differ substantially in the invited and control-group birth-year cohorts. Computer randomisation, however, means these numbers should not differ. Trial times were calculated as date of randomisation until the date the control group had completed the first round of screening. The treatment contrast, however, should be calculated as the difference between the dates screening started in the invited and control groups. Since screening of the control group was completed later than planned, there is bias in favour of screening, especially for the Göteborg trial.5 Giving the numbers of breast-cancer deaths for each trial according to the follow-up model would allow other researchers to do their own analyses. The assessment of cause of death might have been biased in favour of screening in the Two-County trial. There are other important unresolved issues. A meta-analysis from independent researchers is therefore crucial, based on the raw data from all the screening trials, using total mortality as the primary outcome. Peter C Gøtzsche Nordic Cochrane Centre, Rigshospitalet Dept 7112, DK-2100 Copenhagen, Denmark (e-mail: [email protected])
1
2
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist L. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Tabár L, Fagerberg CJ, Gad A, et al. Reduction in mortality from breast cancer after mass screening with mammography. Randomised trial from the Breast Cancer Screening Working Group of the Swedish
THE LANCET • Vol 360 • July 27, 2002 • www.thelancet.com
For personal use. Only reproduce with permission from The Lancet Publishing Group.
CORRESPONDENCE
3
4
5
National Board of Health and Welfare. Lancet 1985; 1: 829–32. Nyström L, Rutqvist LE, Wall S, et al. Breast cancer screening with mammography: overview of Swedish randomised trials. Lancet 1993; 341: 973–78. Miller AB, Baines CJ, To T, Wall C. Canadian National Breast Screening Study, 2: breast cancer detection and death rates among women aged 50 to 59 years. CMAJ 1992; 147: 1477–88. Berry DA. Benefits and risks of screening mammography for women in their forties: a statistical appraisal. J Natl Cancer Inst 1998; 90: 1431–39.
Sir—The updated overview of Lennarth Nyström and colleagues1 addresses many issues raised by Gøtzsche and However, the following Olsen.2 information could provide further reassurance about the validity of the Swedish findings. First, the number of women excluded because of a diagnosis of breast cancer before randomisation in the invited and control groups should have been presented. Although Nyström and colleagues had relied on the data in the Swedish Cancer Registry as the basis of exclusion, if being in the invited group led to more thorough attention that increased the chance of a previous diagnosis being ascertained and registered, there could still be a bias. Such an effect, according to Gøtzsche and Olsen, seemed to have been a problem in the New York trial.3 If similar proportions were excluded in each group in each of the Swedish trials, bias is unlikely. Second, details of the distribution of individual baseline characteristics other than age would have been useful. The availability of such information might be limited if control women were not interviewed at the start of the study. However, certain relevant characteristics may be relatively stable. One example is socioeconomic status, which has prognostic importance in many populations, including the UK.4 K K Cheng Department of Public Health and Epidemiology, University of Birmingham, Public Health Building, Edgbaston, Birmingham B15 2TT, UK (e-mail: [email protected]) 1
2
3
4
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Longterm effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Gøtzsche PC, Olsen O. Is screening for breast cancer with mammography justifiable? Lancet 2000; 355: 129–34. Shapiro S, Venet W, Strax P, Venet L, eds. Periodic screening for breast cancer. Baltimore: Johns Hopkins University Press, 1998. Coleman MP, Babb P, Damiecki P, et al. Cancer survival trends in England and Wales, 1971-1995: deprivation and NHS Region. London: Stationery Office, 1999.
Sir—Lennarth Nyström and colleagues1 present a significant 21% risk reduction in breast-cancer mortality, based on the Swedish randomised controlled mammography trials. The corresponding absolute risk of death from breast cancer in the control groups was 584 (0·0050%) per 117 260 women, and in the intervention groups 511 (0·0039%) per 129 750 women. Based on these numbers, 960 women need to be screened to save one life in 6·5 years. In the age-group with the most favourable results, 55–69 years, the corresponding numbers were 305 (0·0065%) per 46 989 and 240 (0·0045%) per 52 877 women in the control and intervention groups, respectively. 512 women need to be screened to save one life in 6·5 years. To decide whether these findings warrant mammography screening as part of health services financed by the state is a normative question, not a medical one. In democratic societies, people prefer to choose which health services to use. Services not provided by official authorities can be bought on the free market. Under these conditions, the concept of screening is not applicable, as far as reliable criteria for the assessment of screening programmes are concerned. People at greater risk of disease are inclined not to attend, and those who are not offered screening (eg, younger age-groups), buy it if they think they need it. Only if a screening procedure is simple, cheap given the consequences of not providing it, and possible to apply on almost all of the defined target population should it be a task for the state. Gelmon and Olivotto, in their accompanying March 16 Commentary,2 rightly urge more timely and cost-effective procedures than mammography. They are wrong, however, to encourage women aged 55–69 to attend screening. Instead, the detection of breast cancer should be based on proper medical assessment in general practice, and referral when necessary. Pål Gulbrandsen HELTEF Centre for Health Services Research, PO Box 55, 1474 Nordbyhagen, Norway (e-mail: [email protected]) 1
4
Nyström L, Andersson I, Bjurstam N, Frisell J, Nordenskjöld B, Rutqvist LE. Long-term effects of mammography screening: updated overview of the Swedish randomised trials. Lancet 2002; 359: 909–19. Gelmon KA, Olivotto I. The mammography screening debate: time to move on. Lancet 2002; 359: 904–5.
THE LANCET • Vol 360 • July 27, 2002 • www.thelancet.com
Authors’ reply Sir—Laszlo Tabár and colleagues claim that the Östergötland county is currently participating in the overview without the consent of the county’s lead investigator. The trialists of Stockholm and Östergötland, Lars Hellström and Gunnar Fagerberg, retired several years ago and were replaced by Jan Frisell and Bedrich Vitak. Vitak participated in the group initially, then chose to withdraw, but has now announced renewed interest in participating in collaborations. Luc Bonneux notes the differences in the effect of invitation to mammography screening in the Östergötland trial in our overview and in Tabár and colleagues’ follow-up (11 vs 24%). These could be due to different followup times and sources for breast-cancer diagnosis and cause-of-death classification (Swedish Cancer Register vs local endpoint committee). Bonneux also believes that bias may distort the effect of screening. Sticky bias is valid in the prevalence round in the invited group, as seen in the pretrial and trial data for Östergötland (see figure 1 in our report). There was a similar increase in the control group when they were invited to the prevalence round. Sticky bias, however, results only in more conservative estimates. The issue of slippery bias was specifically addressed in our early follow-up of the cause of death pattern through 1989.1 The relative risk of malignant neoplasm in the digestive, respiratory, and urogenital organs, and for leukaemia as underlying cause of death in the invited group compared with the control group was 1·05, 1·02, 0·97, and 1·03, respectively; there was no indication for a slippage towards other cancer sites. Furthermore, during the trial period, patients underwent modern radiotherapy, which has minimal or no risk of cardiac complication. Bonneux finds the effect of the intervention small without considering that in the Swedish trials women were, over an average period of 6·5 years, invited to an average of three rounds. We do not agree. Peter Gøtzsche repeats the criticism from his and Olsen’s previous publications.2,3 Space limitations and the fact that each trial is preparing a separate publication make it look like we focused on only a few questions. Gøtzsche and K K Cheng ask for pretrial background characteristics. No pretrial data were collected in the Swedish trials. We presented pretrial breast-cancer morbidity and mortality
339
For personal use. Only reproduce with permission from The Lancet Publishing Group.