Pii: s0140-6736(99)06065-

Public health
Is screening for breast cancer with mammography justifiable? Background A 1999 study found no decrease in breast- recommended since 1985. The observed decrease in cancer mortality in Sweden, where screening has been number of deaths from breast cancer was 0·8% (not recommended since 1985. We therefore reviewed the significant), whereas the expected decrease was 11%.
methodological quality of the mammography trials and an Although that study can be criticised,12,13 it raises once influential Swedish meta-analysis, and did a meta-analysis again the issue of the reliability of the evidence that We therefore reviewed the methodological quality of the Methods We searched the Cochrane Library for trials and mammography trials and the Swedish meta-analysis, and asked the investigators for further details. Meta-analyses did a meta-analysis ourselves. We focused on the three were done with Review Manager (version 4.0). most important sources of bias in randomised trials: Findings Baseline imbalances were shown for six of the eight suboptimum randomisation methods, lack of masking in identified trials, and inconsistencies in the number of women outcome assessment, and exclusion after randomisation.
randomised were found in four. The two adequately We paid special attention to the quality of the randomised trials found no effect of screening on breast- randomisation, since bias caused by suboptimum cancer mortality (pooled relative risk 1·04 [95% CI 0·84–1·27]) or on total mortality (0·99 [0·94–1·05]). The treatment effects that might be detected if a screening pooled relative risk for breast-cancer mortality for the other trials was 0·75 (0·67–0·83), which was significantly different (p=0·005) from that for the unbiased trials. The Swedish meta-analysis showed a decrease in breast-cancer mortality We searched the Cochrane Library with the terms “breast-neoplasms/all” or “breast next cancer” and “screening” and but also an increase in total mortality (1·06 [1·04–1·08]); “mammography” and extended the search with authors’ names this increase disappeared after adjustment for an imbalance and other terms as appropriate to capture updates of the trials.
When necessary, we asked the investigators for details about the randomisation method, in particular whether the assignment mammography is unjustified. If the Swedish trials are judged process was concealed so that no-one could foresee whichassignment the next cluster or woman would get before actual to be unbiased, the data show that for every 1000 women recruitment. We also asked for baseline characteristics that could screened biennially throughout 12 years, one breast-cancer show whether the screening group was similar to the control death is avoided whereas the total number of deaths is group in terms of important prognostic factors such as age, increased by six. If the Swedish trials (apart from the Malmö symptoms at entry, family history of breast cancer, trial) are judged to be biased, there is no reliable evidence socioeconomic status, and previous examinations for breast that screening decreases breast-cancer mortality.
cancer. We noted whether all randomised women had beenaccounted for in the results and whether the cause of death had been assessed by a panel unaware of screening status. We also sought data on the morbidity associated with screening, definedas reported events that had occurred in at least 100 women. Meta-analyses were done with Review Manager (version 4.0; After heated controversy, there now seems to be general available from http://www.cochrane.dk; accessed on Dec 20, acceptance that the benefit of screening for breast cancer 1999). A fixed-effects model was used unless the test for with mammography has been well documented.1 Large heterogeneity gave p<0·10; 95% CIs are presented.
randomised trials, including a total of half a million women, have been carried out in New York, USA;2Edinburgh, Scotland;3 Randomisation methods and exclusions Kopparberg,7 Östergötland,7 Stockholm,8 and Göteborg9 In the New York trial, pairs of women were matched and in Sweden. A meta-analysis of an update of the five the pairs were randomised.16 The allocation method is not Swedish trials, which used data from individual patients, clear—“every nth woman was placed in the study group, was particularly influential. It showed that screening the paired (n+1) woman in the control group”.16 Because lowered mortality from breast cancer by 29% in women of the matching in pairs, the number of randomised women should be exactly the same in the study group and The findings of a 1999 epidemiological study were in the control group. This was not the case, and the therefore surprising. It found no decrease in breast-cancer number of women is unclear. It has been described as“about 31 000”,16 Nordic Cochrane Centre, Rigshospitalet, Department 7112, 30 23919,20 allocated to the study group, and 30 756,20 Blegdamsvej 9, 2100 Copenhagen Ø, Denmark (P C Gøtzsche MD, 30 765,19 and 30 5652,16 allocated to the control group.
There was also an important imbalance in exclusions after randomisation. Women were excluded if breast cancer had been diagnosed before entry to the trial, and this THE LANCET • Vol 355 • January 8, 2000 status was more completely ascertained for the screened on day 31 of any month were excluded after women; thus, the final study cohort was smaller than the randomisation despite being offered mammography “to control cohort (30 131 vs 30 565).2,16 This difference introduced bias in favour of the screening group. Close approach led to a study group size of 39 164 women. We similarity between the study and control groups has been cannot understand how the number of randomised women in the control group can increase. Some 40-year- characterisics presented in justification for this claim, we old women were excluded from the meta-analysis, which calculated imbalances for previous lump in the breast was based on age at randomisation and not on birth-year (p<0·0001), menopause (p<0·0001), and education cohorts as most of the trials had used, but this exclusion (p=0·05); there were no differences for age, religion, would lead to a decrease as it did for the other three marital status, or pregnancies. These findings are Swedish trials for which we could check the numbers incompatible with an adequate randomisation.
(Malmö Ϫ1·9% vs Ϫ1·9%,6 Kopparberg Ϫ1·3% vs The allocation method of the Edinburgh trial is poorly Ϫ2·0%,31 and Östergötland Ϫ0·2% vs Ϫ0·7%7). We described; 87 general practices were cluster randomised,22 calculated from a table divided into five age categories30 but the allocation was later changed for three of them.23 that the study women in Stockholm were, on average, The screening and control groups differed substantially at 0·18 years younger than the control women (z=2·73, baseline; only 26% of the women in the control group p=0·006, Mann-Whitney test). This imbalance at baseline were in the highest socioeconomic stratum, compared indicated that the randomisation method was inadequate.
In Göteborg, randomisation was partly by day-of-birth randomisation method was grossly inadequate, even for a cluster (18% of participants) and partly individual.9 We calculated from a table divided into 11 age categories9 that In the Canadian trial, women were randomised the study women were, on average, significantly younger than the control women by 0·09 years (z=2·39, p=0·02), allocation lists, in which the intervention was noted on which shows that the randomisation method may have each line. The randomisation could therefore be subverted. However, checking of whether this had Cluster randomisation was used in Kopparberg and happened was also possible, and a thorough review Östergötland.32 The population in these counties was concluded that there could not have been enough cases of divided into 19 blocks which were further divided into two such subversion to affect the reported results.25 Moreover, or three groups on unspecified criteria. These groups were the two compared groups were similar at baseline in terms then randomised. We were unable to find a description of of self-reported symptoms, including lump, family history the randomisation method. In Nyström and colleagues’ of breast cancer, marital status, livebirths, menopause, meta-analysis, the cluster randomisation method was said education, and place of birth.26,27 We found no data on the not to have introduced bias.10 However, the justification for this statement was a reference to an unpublished In the Malmö trial,6 women in each birth-year cohort lecture.10 The meta-analysis is unlikely to have taken the were randomly arranged according to a computer clustering into account, since we obtained the same point program, and those on the first half of the lists were estimate and the same narrow CI for breast-cancer invited for screening (Ingvar Andersson, personal mortality as in the meta-analysis when we based our communication). Thus, the allocation method was analysis on individual women. We therefore used women apparently adequately concealed. No baseline data are as the statistical unit and calculated from a table divided available, but we estimated from the other Swedish trials into eight age categories31 that the study women in that the mean age was similar in the two groups.
Kopparberg were, on average, 0·45 years older than the A sort of continuation of that trial, called Malmö control women (z=5·50, p<0·0001). There was also an Mammographic Screening Trial II,28 has been published imbalance in Östergötland (z=4·04, p<0·0001), the study in brief; it was randomised and had death from breast women being 0·27 years older than the control women.7 cancer as the endpoint, but it did not have a formal The number of randomised women (aged 40–74) is not protocol, and because of an administrative error, all clear: for example, the number in the study group in women born in 1934 were included in the screening group Östergötland has been reported as 39 03432,33 (Ingvar Andersson, personal communication). Because 38 491;7,34 the total number of randomised women in the the report mixes follow-up data from a subgroup of the two trials has been reported as 134 86732 and 133 065.7,34 original trial with data from this new cohort, and since Baseline data were not reported in the Swedish meta- some women were not randomised, the published data analysis.10 3 years after the report was published in The cannot be included in a meta-analysis. No baseline data Lancet, however, a report in a specialist journal stated that the mean age in the screened groups was 55·05 years In the Stockholm trial,8 randomisation was according to compared with 54·54 years in the control groups.35 Since date of birth; women born on days 11–20 of any month the SD for age in the Swedish trials was 10 years,7,31 the constituted the control group. The number of randomised age difference was highly significant (z=12·7, p=3ϫ10Ϫ37).
women is not clear. The number of controls is given as “c.
This extremely skewed distribution is incompatible with 20 000” in an early report,29 and as 19 943 in the final the hypothesis that the women were distributed to the report.8 There is a substantial discrepancy between the screening and control groups according to a truly chance numbers in the final report and the meta-analysis of the Swedish trials10 in which the number of randomised We estimated whether the Malmö trial had an women fell from 40 318 to 38 525 (a decrease of 4·5%) in imbalance at baseline like the other four Swedish trials.
the screening group, but increased from 19 943 to 20 651 We used the number of women as reported in the meta- (a rise of 3·6%) in the control group. This inconsistency analysis and the mean ages as estimated above. We took cannot be explained by the curious fact that women born account of the fact that women in Göteborg were THE LANCET • Vol 355 • January 8, 2000 125 866 in the control groups). Nyström and colleagues did not test whether this increased mortality was significant, nor did they give a CI. They argued that because breast-cancer mortality constitutes less than 5% of the total mortality, such an analysis “would require very large cohorts and is therefore impossible in practice”.35 We based our calculation on number of randomised women (the meta-analysis investigators had used person- years) and found a relative risk of 1·06 (95% CI Table 1: Mammography screening trials according to 1·04–1·08, p<0·0001). The investigators adjusted their calculation for age, after which the relative risk was 1·00.
In The Lancet randomly allocated to study and control groups in the investigators had included the same total numbers of approximate ratio of 1·2 in the 39–49-year age-group and deaths but reported only the age-adjusted risk without 1·6 in the 50–59-year age-group.9 We had no data on age mentioning that an adjustment had been made or that for the 50–59-year group, but since the imbalance in age there was an increased risk of death without adjustment.
in the 39–49-year group was numerically small, we used a The pooled relative-risk estimate for the two unbiased mean age of 54 for both study and control groups. For trials (Malmö and Canada) was 0·99 (0·94–1·05), which Malmö, we used 57 years as estimated mean age in the was very close to the estimate for Malmö alone (0·99 study group, similar to the Kopparberg and Östergötland [0·93–1·05]), since that study reported 3586 deaths, trials.7,31 This approach yielded a mean age in the study compared with only 1147 in Canada (relative risk 1·08 groups of 54·93 years, very close to the 55·05 years reported in the meta-analysis. Since the mean age in thecontrol groups was 0·51 years lower, that in the Malmö control group was estimated to be 56·85 years. The The two trials with adequate randomisation methods and difference of 0·15 years is not significant (z=1·53, p=0·13) baseline comparability (table 1) had similar estimates for which suggests that the randomisation method in Malmö the relative risk of death from breast cancer with 95% CIs was adequate. In summary, our findings suggest that only that overlapped substantially, showing lack of the trials from Malmö and Canada were unbiased (table 1).
heterogeneity (table 2). The combined relative-riskestimate was 1·04 (0·84–1·27).
Diagnosis of deaths from breast cancer The six trials that had not been adequately randomised Knowledge of screening status may affect the judgment of had more favourable outcomes with screening than these cause of death. Masked assessment of cause of death was two trials, and their results were homogeneous (p=0·23 used only in the trials from Canada and Malmö, but in the for test of heterogeneity). The pooled relative risk was Swedish meta-analysis10 all deaths from breast cancer were 0·75 (0·67–0·83). This estimate is significantly different assessed with masking of screening status. Deaths from from that for the two adequately randomised trials breast cancer diagnosed before entry to the trial were generally excluded from analysis. Such exclusions can If the Göteborg trial, which was the least biased trial of lead to bias when the first round of screening identifies the six, was moved from the second group to the first, the cancer in women who have already noted a tumour in relative-risk estimate changed little (0·94 [0·76–1·17]).
their breast if these women are subsequently excluded.
However, since this change creates heterogeneity The New York trial excluded more cancers in the (p=0·08), this trial should probably not be moved. If all screening group than in the control group.
eight trials are analysed together (which would beinappropriate), heterogeneity is also introduced (p=0·05).
All-cause mortalityThe imbalance in age at baseline in the Swedish trials is important. Nyström and colleagues reported in a Total numbers of interventions were identified only in the specialist journal35 that the screened women had an increased risk of death (relative risk 1·05; 15 695 women significantly more common in the screening groups for died of 156 911 in the screening groups vs 11 887 of radical mastectomy (relative risk 1·23 [1·08–1·40]) andfor mastectomy or lumpectomy (1·35 [1·20–1·52], as was radiotherapy (1·25 [1·04–1·50]). A similar tendency was seen in the Canadian trial, in which only surgery done within the framework of the trial was reported. In that trial, the proportion of benign findings in biopsy samples was two to four times higher in the mammography groups throughout the whole screening period.5 We found no data from Edinburgh and New York and data only from the screened group for the other trials.
The effect of screening programmes, if any, is small and the balance between beneficial and harmful effects is verydelicate. It is therefore essential that such programmes are Table 2: Relative risk of death from breast cancer in screenedversus control groups rigorously evaluated in properly randomised trials. THE LANCET • Vol 355 • January 8, 2000 Unfortunately, the randomisation process failed to 3 years before Nyström and colleagues admitted publicly create similar groups in six of the eight trials of that the analysis of total mortality had been adjusted for mammographic screening. Our analyses focused on age as a marker for imbalance, since this variable was the only Another serious flaw in the mammography trials is the baseline information we had available for the Swedish fact that the number of randomised women was inconsistently reported for four of the six trials with Cluster randomisation was used in several of the trials, inadequate randomisation methods. This inconsistency is but the number of clusters was insufficient, which is well not only odd, but it also raises further doubts about the illustrated by the Edinburgh trial.22 The proportions of women in the highest socioeconomic stratum differed The two trials with adequate randomisation found no substantially between the screening and control groups, effect of screening on mortality from breast cancer, not and, as expected, there was a pronounced relation even a tendency towards an effect. By contrast, the pooled between social group and total mortality, which may effect of the six trials with inadequate randomisation was explain why total mortality was much lower in the highly significant. There was no overlap of the CIs for screening group (relative risk 0·85 [0·79–0·92]). Attempts these two effect estimates. This lack of overlap is were made to remedy this shortcoming,3 but adjustments remarkable. Such disparate effects of subgroups of similar cannot fully compensate for faulty methods. First, trials in a meta-analysis are very rare, and a strong adjustment for unknown or unmeasured confounders is warning signal that something is wrong. The explanation impossible. Second, adjustment for one confounder may in such cases is generally methodological. In fact, the create imbalance for another, since confounders are rarely difference between the two point estimates, 1·05 and fully correlated. For example, adjustment for age in the 0·75, is in good agreement with the results from empirical, Swedish trials might seem reasonable; however in the methodological research. Randomised trials with New York trial, age was evenly distributed whereas several inadequate or undescribed allocation methods exaggerate other prognostic factors were not.16,21 Which adjustments the estimated intervention effect by 33–41%, on should then be preferred for that trial? There must have average.14,15 The bias can be even larger in cohort studies.
been many other imbalances in prognostic factors at For example, a meta-analysis of cohort studies of baseline in the Swedish trials, and there is a strong hormone replacement therapy showed protection against probability that other adjustments would have produced coronary heart disease (relative risk 0·50 [0·43–0·56]),40 other results, both more and less extreme than a relative which was not confirmed in a large randomised trial (0·99 risk of 1·05 for the increase in total mortality with [0·80–1·22]);41 again, there was no overlap of the 95% screening. Thus, the third important problem with adjustments is the risk of biased analyses when results of The Canadian trial has been subjected to a fair amount trials which were meant to be randomised but were found of criticism, probably because it had the most negative results of the eight trials. The criticism has been The credibility of the Swedish meta-analysis is greatly rebutted;26 somewhat ironically, this trial seems to be the weakened because it did not report that there were one that is by far the best documented. A persistent important imbalances at baseline in four of the five trials; criticism has been that an effect would be difficult to find that there was increased mortality in the screened groups; because the breasts of all women in the age-group 50–59 and that an adjustment for age had been made without years were physically examined regularly. This criticism is being described.10 The last point is particularly important, unwarranted because mammography will identify many since readers would not have expected any adjustment to tumours that are too small to be detected on physical have been made in a meta-analysis of hundreds of examination alone. Furthermore, any effect of physical thousands of women in which adjustments would not examination is likely to be small. A study of 122 471 change anything, provided that the trials had been women found no effect of regular self-examination of the properly randomised. Shortly after the publication of the breast on breast-cancer mortality after 9 years of follow- meta-analysis, Skrabanek obtained the mortality rates up, even though twice as many of the intervention group from the primary author and drew attention to the consulted an oncologist.42 In addition, Kerlikowske’s increased mortality in the screened groups36 (10·0% vs meta-analysis found that the regular clinical examinations 9·4%; relative risk 1·06). In their response,37 Nyström and in the non-Swedish trials had no influence on the relative Larsson did not mention the imbalance in age, but risk.43 We also much doubt the importance of the fact that defended the relative risk of 1·00 reported in the meta- the Canadian trial was not community based. Proper analysis by comparing the observed number of deaths in randomisation ensures the internal validity of a trial, and if the screened groups with the expected number in the mammography were effective, an effect should also be population (15 695 vs 15 710). They also noted that the seen in a selected part of the population. Finally, the relative risks for total mortality in the individual trials were quality of the mammography has been criticised as being 0·98, 0·98, 0·99, 1·00, and 1·00. It is quite impossible, poor,26 but the tumours found in the Canadian trial were however, to have such rates for the individual trials and smaller, on average, than those found in the Swedish then an increased mortality of 1·06 (as we calculated) for the pooled analysis. Swift38 noted subsequently that “a The study reports provided very few data on morbidity more precise and apt comparison is that between the associated with screening. Some might argue that an mortality rates in the exposed and control groups”. In increased occurrence of surgery, chemotherapy, and response to this indisputable fact Nyström and Larsson radiotherapy in the screened group is only natural and wrote that “we prefer (see our response to Skrabanek) that, in the long run, over decades, the interventions standardised relative risks to crude relative risks”.39 This would become less drastic because the tumours would be reply is remarkable since the whole idea of randomisation detected earlier. However, another point of view is that is to make unbiased analyses possible, but it was another screening would be expected to increase morbidity in the THE LANCET • Vol 355 • January 8, 2000 long run because of false-positive findings, cell changes mammography: overview of Swedish randomised trials. Lancet 1993; that may never develop into cancer, and cancers that will 341: 973–78.
11 Sjönell G, Ståhle L, Hålsokontroller med mammografi minskar inte develop so slowly that the woman dies of other causes dödlighet i bröstcancer. Läkartidningen 1999; 96: 904–13.
12 Rehnqvist N, Rosén M, Karlberg I. Analys av dödligheten kräver helt We could not assess psychological morbidity related to annan metodik. Läkartidningen 1999; 96: 1050–51.
false-positive findings because this feature was not 13 Rutqvist LE. Naturalförloppet, grova metoder ledde till felkalkyl om böstcancer. Läkartidningen 1999; 96: 1210–11.
reported in the trials. In the USA, Elmore and colleagues45 14 Schulz KF, Chalmers I, Hayes RJ, et al. Empirical evidence of bias: estimated that 49% of screened women will experience at dimensions of methodological quality associated with estimates of least one false-positive mammogram during ten screening treatment effects in controlled trials. JAMA 1995; 273: 408–12.
rounds and that 19% will be subjected to biopsy.45 In the 15 Moher D, Pham B, Jones A, et al. Does quality of reports of randomised trials affect estimates of intervention efficacy reported in Swedish trials, false-positive rates of 4–6% have been meta-analyses? Lancet 1998; 352: 609–13.
reported,9,28,29,31 corresponding to an average risk of 40% of 16 Shapiro S, Venet W, Strax P, Venet L, eds. Periodic screening for a false-positive mammogram during ten rounds.
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We conclude that screening for breast cancer with 17 Shapiro S, Strax P, Venet L. Evaluation of periodic breast cancer screening with mammography: methodology and early observations.
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Concurrent use of herbs may mimic, magnify, or oppose the effect of drugs. Plausible cases of herb-drug
interactions include: bleeding when warfarin is combined with ginkgo (Ginkgo biloba), garlic (Allium sativum), dong
quai (Angelica sinensis), or danshen (Salvia miltiorrhiza); mild serotonin syndrome in patients who mix St John’s
wort (Hypericum perforatum) with serotonin-reuptake inhibitors; decreased bioavailability of digoxin, theophylline,
cyclosporin, and phenprocoumon when these drugs are combined with St John’s wort; induction of mania in
depressed patients who mix antidepressants and Panax ginseng; exacerbation of extrapyramidal effects with
neuroleptic drugs and betel nut (Areca catechu); increased risk of hypertension when tricyclic antidepressants are
combined with yohimbine (Pausinystalia yohimbe); potentiation of oral and topical corticosteroids by liquorice
(Glycyrrhiza glabra); decreased blood concentrations of prednisolone when taken with the Chinese herbal product
xaio chai hu tang (sho-saiko-to); and decreased concentrations of phenytoin when combined with the Ayurvedic
syrup shankhapushpi. Anthranoid-containing plants (including senna [Cassia senna] and cascara [Rhamnus
purshiana]) and soluble fibres (including guar gum and psyllium) can decrease the absorption of drugs. Many
reports of herb-drug interactions are sketchy and lack laboratory analysis of suspect preparations. Health-care
practitioners should caution patients against mixing herbs and pharmaceutical drugs.
“Poisons and medicines are oftentimes the same of 1000 elderly people admitted to a hospital from the substances given with different intents.” emergency department found that 538 patients were exposed to 1087 drug-drug interactions; 30 patients Many medicinal herbs and pharmaceutical drugs are experienced adverse effects as a consequence of these therapeutic at one dose and toxic at another.
Interactions between herbs and drugs may increase or common, and to the mixture physicians prescribe, decrease the pharmacological or toxicological effects of patients add various over-the-counter medications, either component. Synergistic therapeutic effects may vitamins, herbs, and foods. All ingested substances have complicate the dosing of long-term medications—eg, herbs traditionally used to decrease glucoseconcentrations in diabetes1 precipitate hypoglycaemia if taken in combination with Sources for this review include MEDLINE 1966–98 (searched under MeSH terms “drug interactions” Herbal medicines are ubiquitous: the dearth of reports combined with “herbal medicine”, “traditional of adverse events and interactions probably reflects a medicine”, “Chinese traditional medicine”, “African combination of under-reporting and the benign nature of traditional medicine”, “Ayurvedic medicine”, “Oriental most herbs used. Experimental data in the field of herb- traditional medicine”, “Unani medicine”, and “Arabic drug interactions are limited, case reports scarce, and medicine”); EMBASE 1994–99 (searched under the case series rare. This lack of data is also true of drug- same terms); reference dredging; and my own files on drug interactions: published clinical studies are mainly case reports (controlled trials are scarce, since the Many reports of herb-induced interactions lack crucial random assignment of patients to trials that examine documentation on temporal relations and concomitant unintended effects is not ethical). The true prevalence of drug use. Perhaps the most serious problem encountered drug interactions is substantial but unknown. One study in analysing such reports is the consistent absence of anyeffort (beyond that of reading the label) to establish a positive identification of the herb involved, and toexclude the effect of contaminants or adulterants. Unless George Washington University School of Medicine and Health noted otherwise, the reports mentioned herein did not Sciences, Department of Health Care Sciences, 2150 PennsylvaniaAvenue, NW 2B-417, Washington, DC 20037, USA This review was limited to the most commonly used medicinal plants, and to clinical reports (animal studies THE LANCET • Vol 355 • January 8, 2000

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