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Systematic review of screening for breast cancer with mammography

Ole Olsen, deputy director, senior researcher, MSc

Peter C. Gøtzsche, director, MD, MSc

The Nordic Cochrane Centre

Rigshospitalet, dept 7112

Blegdamsvej 9

DK-2100 København Ø

Denmark

e-mail: [email protected]

Tel: +45 3545 5571

Fax: +45 3545 7007

Published October 20, 2001

SynopsisMammographic screening is of uncertain benefit and leads to greater use of more aggressive treatment. Bydetecting cancers early, mammographic screening is widely believed to lead to reduced mortality from breastcancer and to less aggressive treatment. Half a million women have participated in randomised trialsworldwide. This review failed to find a decrease in overall mortality, and the best trials also failed to find areduction in breast cancer mortality. The review found that screening leads to more aggressive treatment.

AbstractBackground

Mammographic screening for breast cancer is controversial, as reflected in greatly varying national policies.

Objectives

To assess the effect of screening for breast cancer with mammography on mortality and morbidity.

Search strategy

MEDLINE (16 May 2000), the Cochrane Breast Cancer Group's trial register (24 Jan 2000) and referencelists. Letters, abstracts and unpublished trials. Authors were contacted.

Selection criteria

Randomised trials comparing mammographic screening with no mammographic screening.

Data collection & analysis

Data were extracted by both authors independently.

Main results

Seven completed and eligible trials involving half a million women were identified. The two best trialsprovided medium-quality data and, when combined, yield a relative risk for overall mortality of 1.00 (95%


CI 0.96–1.05) after 13 years. However, the trials are underpowered for all-cause mortality, and confidenceintervals include a possible worthwhile effect as well as a possible detrimental effect.

Breast cancer mortality is an unreliable outcome that is biased in favour of screening. Flaws are due todifferential exclusion of women with breast cancer from analysis and differential misclassification of causeof death. The best trials failed to show a significant reduction in breast cancer mortality with a relative risk of0.97 (95% CI 0.82–1.14). The numbers of mastectomies and tumourectomies and the number of women whoreceived radiotherapy were significantly higher in the screened groups.

Reviewers' conclusions

The currently available reliable evidence does not show a survival benefit of mass screening for breast cancer(and the evidence is inconclusive for breast cancer mortality), whereas it has shown that mass screening leadsto increased use of aggressive treatment. Women, clinicians and policy makers should consider thesefindings carefully when they decide whether or not to attend or support screening programs.

BackgroundBreast cancer is a common cause of death among middle-aged women. Early detection through massscreening with mammography has been introduced in many countries in the hope that early interventionwould lead to reduced mortality and less aggressive treatment. However, as screening primarily seems toidentify slow-growing tumours (1,2), the adverse effects of treatment could potentially reduce or evenneutralise any possible benefits.

As the expected benefit of screening is relatively small, the only reliable way to test its effectiveness is withrandomised trials. Large trials, involving a total of half a million women, have been carried out in NorthAmerica and Europe (3-11) and others are ongoing (12,13). Several meta-analyses have been published(11,14-29) and an update of the Swedish trials, which used individual patient data, showed that the mortalityfrom breast cancer was reduced by 29% in women aged 50–69 years (11).

This has led many to believe that the benefit of mass screening for breast cancer with mammography is welldocumented. However, some countries have abstained from introducing screening and some commentatorshave felt that the lack of a documented reduction in all-cause mortality was important (30-32). Thescepticism is supported by the prediction that radiotherapy treatment of women at low risk, such as thosewho have their cancers identified at screening, will increase overall mortality (33,34), primarily because ofcardiovascular adverse effects. This illustrates that it is essential to ascertain that an apparent reduction inbreast cancer deaths is not due to relabelling of cause of death among breast cancer cases.

Meta-analyses of screening are often deficient in their reporting of methods (35), and few of the meta-analyses listed above have attempted to take account of trial quality. We previously critically assessed thebreast screening trials (27,36), identifying important biases and other weaknesses in most of the trials. Weconcluded that mass screening was unjustified, since the two trials which were methodologically most soundhad failed to find an effect on breast cancer mortality. We report here a more detailed systematic review ofthe trials.

ObjectivesTo study the effect of screening for breast cancer with mammography on mortality and morbidity.

Criteria for considering studies for this reviewTypes of studies

Randomised and quasi-randomised clinical trials. Trials using less reliable methods were evaluatedseparately.

Types of participants

Women without previously diagnosed breast cancer.


Types of interventions

Experimental: screening with mammography.

Control: no screening with mammography.

Types of outcome measures

Overall mortality.

Mortality from breast cancer.

Mortality from any cancer.

Use of surgical interventions.

Use of adjuvant therapy.

Adverse effects of mammography, for example, related to false positive findings.

Search strategy for identification of studiesWe used a very broad search strategy, as there are thousands of papers describing or commenting on thescreening trials, few of which are traditional trial reports. We searched MEDLINE with (exp breastneoplasms/all OR "breast cancer" OR exp mammography/all OR mammograph*) AND (exp massscreening/all OR screen*). This search was supplemented with a search on 11 common author names(Alexander-F*, Andersson-I*, Baines-C*, Bjurstam-N*, Duffy-S*, Fagerberg-G*, Frisell-J*, Miller-AB,Nystrom-L*, Shapiro-S, Tabar-L*). The latest search was done on 16 May 2000; 10 446 records wereretrieved and imported into ProCite where they were searched for author names, cities and eponyms for thestudies. The MEDLINE searches are updated annually.

Reference lists were scanned for additional publications on the trials. Further, the specialised registermaintained by the secretariat of the Cochrane Breast Cancer Group was searched (24 Jan 2000) (details of thesearch strategy applied to MEDLINE for the register is outlined in the group's module).

Letters, abstracts and grey literature were accepted in an attempt to minimise the impact of publication biasand to retrieve as much relevant information as possible.

Methods of the reviewStudy selection

Decisions on which trials to include were made independently by the two reviewers on the basis of themethods of the trials. Disagreements were resolved by discussion. An inclusive strategy was preferred; wedivided the trials on the basis of their quality rather than omitting some of them.

Assessment of quality of studies

If the randomisation is flawed such that the mammography and control groups cannot be compared, the trialcannot provide reliable evidence. In contrast, if exclusions and re-allocations are biased, it may be possible touse the trial if outcome data can be provided by the trialists for all the women as originally randomised.

We initially focussed on the randomisation process, baseline comparability, exclusions after randomisation,and consistency in the reported numbers of women randomised (27). The authors of each trial were informedabout the outcome of our initial assessment and were asked for additional information. We then classified theavailable data according to a) whether the randomisation was adequate and led to comparable groups; b)post-randomisation exclusions were few or unbiased; and c) reliable outcome data were available. Data wereclassified in four groups:

1. High-quality data: all criteria fulfilled.

2. Medium-quality data: only minor violations, important bias not suspected, or could be corrected.


3. Poor-quality data: major violations, important bias suspected and could not be corrected with availabledata.

4. Flawed data: major violations, important bias documented and could not be corrected.

Assignment of trials into one of the categories was carried out by the reviewers.

Data extraction

Main outcome data were extracted independently by the two reviewers; disagreements were resolved bydiscussion. Extracted data included: number of women randomised , the randomisation and blindingprocedures, exclusions after randomisation, type of mammography, number of screenings and intervalbetween screenings, attendance rate, contamination caused by mammography in the control group, co-interventions, overall mortality, mortality for breast cancer, mortality for any cancer, use of surgicalinterventions, chemotherapy, radiotherapy, tamoxifen and other adjuvant therapy, and adverse effects ofmammography (for example, related to false positive findings). We contacted the primary investigators toclarify uncertainties.

Statistics

Intention-to-treat analyses were conducted. A fixed effects model was used, and 95% confidence intervals(CI) are presented. In case of heterogeneity (p<0.10), the reasons for this were explored.

The trials with poor-quality data and the flawed trials presented particular problems. We could not carry out aproper analysis for all-cause mortality as we did not have access to the necessary data (see Methodologicalquality of included studies). For the sake of completeness, and in view of the comments from the CochraneBreast Cancer Group editors, the raw data are presented in the graphs. Data from the flawed studies arepresented in a separate graph. Although the estimates we obtained are not formally correct for the poor-quality and flawed trials, they turned out to be in close agreement with the estimates and confidence intervalspublished by the trialists for breast cancer mortality. We have shown the results for each of the quality groupsseparately. We report outcome data as closely as possible to the average follow-ups of 7 and 13 years, whichwere the most common intervals presented in the trial reports, and used age groups over 50 and under 50years, which is the limit that has most often been used in the literature.

Description of studiesWe identified nine trials (3-13). Some of the trials were divided into slightly different subtrials. The Two-County trial had different randomisation ratios in the two counties (37,38); the Edinburgh and Malmö trialscontinued to include women as they passed the lower age limit for entry to the trial; the Canadian trialcovered the age groups 40–49 years (7) and 50–59 years (8), with slightly different co-interventions in theform of physical breast examination. Most trials covered the age range 45–64 years. The Canadian study wasthe only one in which the women were individually randomised after having given their informed consent.The other trials were based on a prespecified segment of the female population that was randomised toinvitation for screening or to a control group. The UK age trial and the Singapore trial have not yet publishedany mortality data.

By definition the intervention always included mammographic screening. In the Two-County study thescreened women were, in addition, encouraged to perform breast self-examinations once a month on a fixeddate (39). Physical examinations of screened women were also performed in New York and Edinburgh. InCanada, in the 40- to 49-year age group, screened women had an annual clinical examination,whereas controlwomen were examined at the first visit and were taught self-examination for use thereafter. In the 50- to 59-year age group, all women had their breasts examined annually. Thus, the treatment contrast consisted ofonly mammographic screening in four trials (4,8-10), whereas it included various degrees of physicalexamination in addition to mammographic screening in another four (3,5-7). The duration of the screeningintervention fell in the range 3 to 16 years and was followed by general screening including the control groupin all trials except the Canadian one. The New York trial was not immediately followed by screening (40);the control women in the Edinburgh trial were invited for screening in their tenth year of follow-up. The


Malmö trial had more than 12 years of follow-up before the control group was invited for screening; theother Swedish trials were contaminated by early introduction of systematic screening in the control group(see below). The number of consecutive screening invitations was in the range four to nine for all trialsexcept the Two-County and Stockholm trials, in which a large fraction was invited for only two or threescreenings.

In all trials women in the control groups were offered usual care. This included mammography on indication,that is, in case of suspected malignancy, with the probable exceptions of the New York trial and the first fiveyears of the Two-County study.

The technical quality of the mammograms and the observer variation seem only to have been fully assessedin the Canadian trial. It is therefore not possible to compare the technical quality between trials apart fromtheir reported sensitivities and specificities. Various combinations of one- and two-view mammography wereused (see Table 1: Characteristics of included studies).

Methodological quality of included studiesThe studies have been conducted and reported over a long period of time during which standards forreporting trials have changed (41). The New York study, for example, was first reported in 1966 (3), butcrucial details on the randomisation method, exclusions and blinding were published with a delay of 20 years(42-44). It also took almost 20 years before data on use of radiotherapy and chemotherapy in the Kopparbergtrial were published (45). We have devoted considerable space to discussing each trial, because it isimportant for understanding their limitations and because the information presented has not beensystematically assembled and analysed previously. The trials are described in chronological order; theirquality is briefly summarised in Table 2.

The New York trial

This trial invited women aged 40–64 years. It used an adequate randomisation mechanism with individualallocation within pairs matched by age, family size and employment group (42). Entry dates into the trialwere the dates the women were scheduled for the examination (3); control women were assigned the sameentry dates as their matched study group women (42). Enrolment ran from December 1963 to June 1966.However, postrandomisation exclusions occurred and we calculated imbalances at baseline. The groups werenot balanced for previous lump in the breast (p<0.0001), menopause (p<0.0001), and education (p=0.05)while there were no significant differences for age, religion, marital status, or pregnancies (27). Furthermore,the matched pairs method should lead to intervention and control groups of exactly the same size. This issupported by the approximate numbers given in several publications, e.g. "The women were carefully chosenas 31 000 matched pairs" (46). The largest published exact number of women invited was 31 092 (47) butoutcome data relate to fewer women. Women with previous breast cancer were excluded, but women in thecontrol group "were identified through other sources as having had breast cancer diagnosed before their entrydates" and this status "was most completely ascertained for screened women" (44). Based on information inthe trial reports (42,47,48) we calculated that 853 (31 092 – 30 239) women were excluded from the screenedgroup because of previous breast cancer, compared with only 336 (31 092 – 30 756) in the control group.This would be expected to create bias. If only 10% of these excluded breast cancer cases are added as breastcancer deaths after 18 years of follow-up, the breast cancer mortality becomes higher in the screened groupthan in the control group, since the difference in breast cancer mortality at that time was 44 deaths (49).

We found no data on the autopsy rate. Cause-of-death assessments were unblinded for 72% of the women;the remaining 144 cases (71 from the study group and 73 from the control group) were considered dubiousand were reviewed blindly (44). Two to seven times (depending on the classification) more deaths wereclassified as caused by breast cancer in the control group than in the screened group. Based on theclassification in the control group, there were 21 fewer cases than expected classified as breast cancer deathsin the screened group (p=0.0003). Differential misclassification might therefore be responsible forapproximately half of the reported mortality benefit (44 deaths) (49).


For both reasons, the reported breast cancer mortality seems to be unreliable, but as the trial was adequatelyrandomised, it may provide reliable data on overall mortality. The principal investigator supplied somehelpful information (Shapiro, personal communication,18 June 1999); a co-investigator has confirmed that hehas access to the data (Prorok, personal communication, 2 Feb 2000) but has not confirmed whether data willbe obtainable for all randomised women. The published data are flawed.

The Malmö trial

This trial recruited women aged 45–49 years. It was adequately randomised by computer on an individualbasis within each year of birth (50) dividing a randomly arranged list in the middle (Andersson, personalcommunication, 15 June 1999). This should lead to screening and control groups of equal size, or at least notdiffering by more than one woman per birth year cohort. Accordingly, it was noted in the first publicationsthat 21 242 women were randomised to the screening group and 21 240 to the control group (51,52).

A later publication in Swedish reported that the control group was 21 244 (53). The main publication fromthe trial (4) reported on only 21 088 women in the study group and 21 195 in the control group, but did notaccount for the missing women. In the 45–50 years age group, 137 are missing from the intervention groupand 26 or 27 from the control group, mainly because the 1929 birth year cohort was recruited by anindependent research project which included mammography (Andersson, personal communication, 12 Feb2001). The trialists recruited less than half of the planned birth year cohort but this does not explain why 26or 27 women are missing from the control group. Furthermore, differences in numbers of missing womenamount to up to 23 women in the reported 5- and 10-year age groups, and in one group 2 additional womenoccur. Only in a minority of age and intervention groups are the deviations below the expected maximum of5 (one per birth year cohort). It is not clear why these women are missing, when they were lost, or whetherthey died from breast cancer or other causes (54).

The imbalance in the numbers of missing women are also of concern because the date of entry into the trialwas defined differently for the two groups. It was not the date of randomisation but the date of invitation forthe intervention group (4). The midpoint of these dates for each birth year cohort defined the date of entry forwomen in the control group (Andersson, personal communication, 10 Oct 2000). Enrolment began inOctober 1976 (Andersson, personal communication, 10 Oct 2000) and ended in September 1978 (4).Screening of the control group began in December 1990 (29). In a meta-analysis of the Swedish trials (11),breast cancer cases diagnosed before randomisation were explicitly excluded, further reducing the screenedgroup by 393 and the control group by 412. This step seems unbiased as it involved an official register, but intotal 86 more women were excluded from the screened group than the control group. Baseline age data werenot significantly different in the screened group and the control group (36).

The autopsy rate for breast cancer cases as related in the main publication for this trial (4) was high, 76%, butit was halved from 1985 to 1997 (Andersson, personal communication, 10 Oct 2000). Cause-of-deathassessments were blinded for women with a diagnosis of breast cancer up to 1988 (Andersson, personalcommunication, 10 Oct 2000).

Because of the missing women, the published data may not be fully reliable, but as it was possible to do asensitivity analysis including them, we classified the data as of medium quality. Exclusion of the entire 1929birth year cohort from analysis changes the relative risk for death from breast cancer by 0.01 (Andersson,personal communication, 12 Feb 2001).

A continuation of the Malmö trial, MMST II (55), was not conducted according to a formal protocol and hasbeen published only in brief. Because of an administrative error, one total birth year cohort (1934) wasinvited for screening (Andersson, personal communication, 21 June 1999). We therefore cannot checkwhether the other cohorts were adequately randomised or whether there were differential postrandomisationexclusions. No baseline data are available. It is not clear why the trial was neither included nor mentioned inthe Swedish meta-analysis, nor is it clear to what extent cause-of-death assessments were blinded as in themain trial. As the trial report mixes follow-up data from a young subgroup of the original trial with data fromthis new cohort, also of young women, the published data cannot be used in a meta-analysis. Exclusion of the


entire 1934 birth year cohort from analysis changes the relative risk for death from breast cancer by 0.01(Andersson, personal communication, 12 Feb 2001). We classified the available data as of poor quality.

The Two-County trial

This trial is an amalgamation of the Kopparberg and Östergötland trials that recruited women 40 years of ageand over. The studies were age-matched, cluster randomised trials (21 and 24 clusters, respectively), in whichthe selection was stratified to ensure an even distribution between the two groups with respect to residency(urban or rural), socioeconomic factors and size (5,37,38). The randomisation process and the definition ofthe date of entry into the trial have been inconsistently described. According to the first publications, randomallocations of the women in each community block took place three to four weeks before screening started(56), and all women from a given block entered the study at the same time (5); date of entry was taken as thedate of randomisation (5). However, a recent thesis noted that a notary public (Landstingsrådet CurtHägglund) allocated the clusters in Östergötland by tossing a coin (29) while witnesses were present(Fagerberg, personal communication, undated). In the thesis, a reference is given to the creation of clustersbut this reference is missing from the thesis (29). Nyström sent us a draft memo, which suggested a possiblecreation of clusters in Östergötland (the number of suggested clusters was different from the finally appliednumber). Thus it is not clear whether the randomisation was carried out on only one occasion or whether ittook place over several years. We have been unable to find any detailed description of the randomisation inKopparberg.

As a consequence the definition of entry dates into the trial is unclear. Women were invited to their firstscreening from October 1977 to January 1980 in Kopparberg (57). The cohorts in Östergötland were definedbetween May 1978 and March 1981. It is not clear how many women were randomised. After receivingmagnetic tapes from the investigators, Nyström reported that 92 872 women were randomised inÖstergötland (29). However, most trial reports refer to a larger number of women, 92 934 (58-60), althoughtheir reported age group is smaller than Nyström's. We found the same discrepancy for Kopparberg. Baselinedata potentially affecting mortality exist (61) but although documentation of baseline comparability wascalled for in 1988 (54), this appears not to have been published. The randomisation procedure may have beenseriously flawed:

1) The breast cancer mortality rate in the control group in Kopparberg is higher than that in the control groupin Östergötland (0.0021 vs 0.0012, p=0.02). This is not apparent from the tabulated data (5), but was pointedout to us by Friederike M. Perl. The published graphs are also misleading: The adjacent mortality curves lookmuch the same but this is because the two y-axes are differently scaled (62).

2) There are more pretrial breast cancers in the control group areas in Kopparberg than in the interventiongroup areas. Women with previous breast cancer were partly excluded from the early analyses and fullyexcluded in later publications. The procedure is unclear, e.g. it is not described how the diagnosticinformation was obtained in the two groups (63). The number of women excluded is not stated explicitly, butcan be calculated by subtracting numbers in table 1 in a later publication (63) from those in table 1 in anearlier one (5). There is an excess of excluded women in the control group with more than half of this excessoccurring in the age group 60–69 in Kopparberg (p=0.007).

3) There is a difference in age distribution. Although age-matching was reported (37,57,64), the studywomen in Kopparberg were, on average, 0.45 years older than the control women and in Östergötland theywere 0.27 years older (27).

High correlations within the geographically defined clusters may be expected for age and socioeconomicvariables. In order to test whether baseline differences are too large to be ascribed to chance, the distributionfor all baseline variables for each of the 45 clusters is therefore needed.

The autopsy rate was 36% (65). Cause-of-death assessments were not blind. In a meta-analysis of theSwedish trials, a blinded independent endpoint committee reassessed the death classifications (11).


Information on when systematic screening of the control group started is contradictory. In the Swedishlanguage protocol, a five-year intervention period was planned but with a stopping rule based on statisticalsignificance testing every six months (39). The five-year period, with screening twice, was confirmed in apaper published while the trial was ongoing, but the sequential testing was not mentioned (37). The mainpublication of the trial in The Lancet (5) mentions neither the five-year intervention period, nor the sequentialanalysis, but that some women under 50 years of age received four invitations to screening. On screening inthe control group it is stated that "13% of women in the control group had a mammographic examination aspart of routine medical care up to the end of 1984. Most of these examinations were in 1983–84". The readeris left with the impression that no systematic screening had been introduced in the control group, which isconfirmed later when it was stated that screening was offered to the control group after publication of theresults in 1985 (66).

However, the pre-planned five-year period is indirectly confirmed in the Swedish meta-analysis (11, figure4), which indicates that screening started as early as 1983 in Kopparberg. In a recent thesis, the starting datewas September 1982 (29). For Östergötland, these dates are 1984 and April 1986, respectively. This suggeststhat control group women who received mammography during 1983–84 did not do so as part of routinemedical care but as part of a screening program, and that the information given in The Lancet was incorrect.

For Östergötland, a decision was made in 1986 to screen all women and the screening was carried out in1987–1988 (67), which is later than indicated in the Swedish meta-analysis (11) but in accordance with thethesis (29). Thus, the range of the discrepancies amounts to 3 years for both counties, but it seems thatscreening of the control group in Kopparberg started in 1982 in accordance with the protocol and the thesis,and in Östergötland in 1986.

No information is available from the primary author of this trial who has refused further collaboration notonly with us but with other breast screening trialists in Sweden and in the United States (68) (Tabar, personalcommunication 17 Jan 2000; and Prorok, personal communication 2 Feb 2000). We have not receivedinformation from Nyström either on the missing account of the randomisation process in Kopparberg.Nyström has admitted that our criticism (27) "of the presentation of the randomisation process in the Two-County trial is justified" (29). We believe, however, that it is not only the presentation that is faulty andwonder why crucial details on this study have still not been published, although they do exist (61).

The final assessment of the validity of the Two-County trial awaits clarification from Socialstyrelsen, whichfunded the study and which we contacted 4 Sept 2000. We classified the published data as of poor qualityand very likely flawed.

The Edinburgh trial

This was a cluster randomised trial with about 87 clusters (the number varies in different reports), and the agegroup was 45–64 years (6). Coded general practices were stratified by size and allocated by manualapplication of random numbers. Of the 15 practices initially randomised to the screening group in the Southdistrict, at least three later changed allocation status and at least four others were added (69); in total, sevenpractices changed allocation status (practices operating from the same premises were given the same trialstatus, two practices were unintentionally told the wrong status, and three changed because of "statisticalconsiderations") (70). One practice was included in the follow-up even though it was a pilot screeningpractice that did not participate in the randomisation (71). The trialists have normally conducted replicateanalyses with these women removed (Alexander, personal communication, 3 Oct 2000) but these data seemnot to have been published.

Doubts about the outcome of the randomisation procedure have been raised by the trialists (69), supported bybaseline differences: 26% of the women in the control group and 53% in the screening group belonged to thehighest socioeconomic level (6). Furthermore, mammographic screening seemed to cause a highly significant26% reduction in cardiovascular mortality which is unlikely (69). Entry dates into the trial were defineddifferently in the screening and control groups. In all but five practices , women suitable for invitation toscreening had an entry date which was the date the invitation letter was issued. Eligible women in hospital


etc. were given an entry date corresponding to the date their names appeared on the list sent to their generalpractitioner. We have not been able to find the definition of entry dates for the remaining 5 practices. In thecontrol group the entry date for a woman was the date on which her physician's practice was indexed. Beforeentry, the general practitioners in the screening practices had to decide whether each woman would besuitable for invitation to screening. Physicians in the control practices decided whether each woman wouldbe eligible to receive a leaflet about breast self-examination (70). The eligibility criteria are thus broader forthe control group and the entry dates seem to be earlier. Practices were enrolled one at a time over a period of2.5 years, from 1979 to 1981 (69); women turning 45 and women moving into the city were enrolled on anongoing basis (70). Screening of the control group began in the tenth year of follow-up (6). The exclusionprocedures were different in the study and control groups (70,72); 338 women and 177 in the control groupwith a previous diagnosis of breast cancer were excluded from the study group (6). We found no data onautopsy rate. The trial is flawed.

The Canadian trial

This trial appears to have been adequately randomised (7,8). Women aged 40–59 years were allocatedindividually; the entry date into the trial is therefore the day of randomisation. Their names were enteredsuccessively on allocation lists, where the intervention was prespecified on each line. An independentthorough review of ways in which the randomisation could have been subverted uncovered no evidence of it(73). Enrolment took place from January 1980 to March 1985; the year with most women enrolled (32%)was 1984 (7). Postrandomisation exclusions were few and balanced between the groups. No women wereexcluded because of previous breast cancer. In the age group 40–49 years (7), 42 women were excluded, 25because of protocol violations. In the age group 50–59 years (8), 71 were excluded of whom 32 were totalrefusers who demanded to have their study records destroyed. In the latest publication from this trial, thenumber of excluded women is 54, with similar numbers and reasons in the two groups (74). Data showsimilar numbers and reasons also for the age group 40–49 years (Miller, personal communication, 18 Jan2001). The validity of the randomisation procedure is supported by the nearly identical size of thecomparison groups (25 214 vs 25 216 aged 40–49 years and 19 711 vs 19 694 aged 50–59 years and thecomparability at baseline in age and nine other factors of potential prognostic importance (7,8,74,75). Therewere more small node-positive cancers in the screened group than in the control group among women aged40-49, but this is a post-hoc subgroup finding which is probably a result of the intervention, and exclusion ofthe deaths caused by these cancers does not change the result (7,76,77). The autopsy rate was low, 6% amongbreast cancer cases (Baines, personal communication, 18 Jan 2001). Cause-of-death assessments wereblinded for women with diagnosed breast cancer and for other possible breast cancer deaths. The Canadiantrial provides medium-quality data.

The Stockholm trial

This trial is technically two trials with partly overlapping control groups. The first trial comprises womenaged 40–64 years in 1981 (born 1917–1941) (9). Women born on days 1–10 in a month were invited forscreening, and those born on days 11–20 were controls. The second trial comprises women aged 40–64 yearsin 1982 (born 1918–1942). Women born on days 21–30 were invited for screening, those born on days 11–20were controls. As there are no dates of randomisation, it is important that the dates of entry into the twogroups are comparable.

The cohort for the first trial was probably defined in January 1981 (78) (Frisell, personal communication, 16Nov 2000), although March 1981 has also been mentioned (79). Invitations were sent successively byascending order of birth date (79). The date of entry was defined as the date of invitation (80). Invited womenborn on the first day in a month were matched (as a group) to control women born on the eleventh, womenborn on the second were matched to women born on the twelfth, etc. The recruitment procedure tookapproximately 1 year and lasted from 9 or 13 March 1981 (Frisell, personal communications, 13 and 16 Nov2000) to 26 April 1982. It is not clear when the second cohort was defined, but invitation for screening beganon 28 April 1982 and lasted until 20 May 1983 (Frisell, personal communication, 13 Nov 2000). The control


women born in 1918–1941 were used twice (Frisell, personal communication, 16 Nov 2000), once in eachsubtrial, and should therefore have two entry dates, approximately 1 year apart.

According to the matching, there should be a similar number of women in the screened and control groups.However, we calculated a significant imbalance in the second subtrial (p=0.01, Poisson analysis), with 508more women belonging to the screened group than to the control group (80). This indicates that therandomisation in the second round was inadequate. The reported numbers of women in the various subgroupsare inconsistent, as are the numbers reported to us in personal communications (Frisell, personalcommunications, 13 Nov 2000; 16 Nov 2000). Because of the problems related to timing and the substantialoverlap of the two control groups, results from the two subtrials are not independent, and the estimatescannot be pooled without correction for dependence. It is not clear how these difficulties were handled in thetrialists' analysis (80), and we cannot find any description of the method applied in the Swedish meta-analyses either (11,29). We suspect the trial has been analysed as a cohort study and not as a randomised trialbecause there are more women in the control group than would be expected from the matching. Furthermore,even using the numbers as reported, there are too few person–years in the screened group, for example,19 000 too few after seven years of follow-up (11), which is close to one year per woman. This indicates thatthe data have been analysed erroneously. Age is the only baseline information we have found, and accordingto our revised calculations, there are no significant age differences within the two subcohorts.

The autopsy rate was 22% (29). The first publication on breast cancer mortality reported no women excludedafter randomisation, but only breast cancer cases identified during the intervention period were followed upto ascertain breast cancer deaths (80). In later publications, exclusions were reported, but no numbers weregiven (11,29,81). The numbers of exclusions we have been able to derive from personal communicationshave been inconsistent (Frisell, personal communications, 13 Nov 2000; 16 Nov 2000). Information on whenscreening of the control group started is contradictory. According to the trialists, the controlled design of thestudy was stopped after 1985, and during 1986 the control women were invited to screening mammography(80), giving an intervention contrast of five years in the first subtrial and four years in the second. However,in a recent thesis, the starting date was earlier, October 1985 (29), and it appears from a figure (11) that a fewwomen were screened after three years and most after four years. A valid comparison of benefits and harmsof screening should be restricted to this period (80). It is not stated whether cause-of-death assessments wereblinded for this initial period. We classified the data published by the trialists and in the Swedish meta-analyses as of poor quality.

The Göteborg trial

This trial includes women aged 39–59 years, but only results for women aged 39–49 years have beenreported in an original paper (10). The randomisation was done by the city municipality's computerdepartment. In the first publications, average randomisation ratios were mentioned. Birth year cohorts wererandomised successively with the ratio adjusted according to the capacity of the screening unit (Bjurstam,personal communication, 10 Oct 2000). According to the trial report, women were randomised in the ratio1:1.2 in the 39- to 49-year age group and 1:1.6 in the 50- to 59-year age group, according to day of birth inthe calendar cohorts 1933–1935 and by computer for the cohorts 1936–1944. Additional information allowedus to calculate the randomisation ratios for the three oldest cohorts; these ratios were 1:1.5 for the 1933cohort and 1.18 for the 1934 and 1935 cohorts (82). The changing randomisation ratios appear to be inreasonable agreement with the observed ratios (1.39, 1.11 and 1.11, respectively, in the corresponding agegroups 49, 48 and 47). In the other age groups, the randomisation ratio varies considerably, for example,1:1.12 for ages 44, 45 and 46 and 1:1.3 for the age group 39–43. Thus, the randomisation ratios seem to varyby about 30% in the age group 39–49; the variability of the randomisation ratios in the age group 50–59 hasnot been described. The trial may have been well randomised but further information is needed to check this.

A correct analysis would need to take the irregular randomisation into account, but we await the full reporton women aged 50–59 (Bjurstam, personal communication, 10 Oct 2000). We found baseline data only onage, and since the allocation ratios are so irregular, we cannot check whether the groups were comparable.Entry dates are not defined but the birth year cohorts were randomised one at a time, beginning with the 1923


cohort in December 1982 and ending in April 1984 with the 1944 cohort, who received their first invitationin May 1984. A similar proportion of women were excluded from the study and the control groups, 254(1.2%) and 357 (1.2%), because of previous breast cancer (Bjurstam, personal communication, 10 Oct 2000).According to the trialists the control group was invited for screening after 6–7 years (10), that is, December1988 at the earliest. However, in a recent thesis, the starting date was November 1987 (29) and an earlierpaper (11, figure) indicated that half of the women were screened after three years and most of the rest aftersix years. A valid comparison of benefits and harms of screening should be confined to the period prior toscreening of the control group. A full trial report for the 50–59 year age group has not been submitted forpublication despite the fact that the trial began in 1982. The selectively reported data for the 39–49 age groupcould therefore represent an instance of publication bias. It is not clear whether the varying randomisationratios have been properly accounted for in the published analyses. The autopsy rate was 31% (29). Weclassified the available data as of poor quality.

Sources of data used for the meta-analyses (see graphs)

Overall mortality: (4,7,8,10,29,43,63,65,71,74,83); deaths ascribed to breast cancer: (4,7,8,10,11,40,62,71,74,81,83-88); mortality among breast cancer patients: (86); deaths ascribed to cancer, allpatients (4,43,44,74,86,88); mastectomies and tumourectomies (4,9,45,89,90); radiotherapy (4,45,89,91);chemotherapy and hormone therapy (4,45).

ResultsWe included seven trials. No trials with published high-quality data were identified; two trials were classifiedas having medium-quality data (Canada and Malmö) and three as having poor-quality data (Göteborg,Stockholm and Two-County). The remaining two trials (Edinburgh and New York) were flawed, and theirresults are therefore shown in a separate graph, without any summary estimates.

Overall mortality (graphs, outcomes 2-7)

Mass screening for breast cancer did not change overall mortality significantly. Relative risk (RR) for thetrials with medium-quality data was 0.99 (95% CI 0.94–1.05) after seven years and 1.00 (0.96–1.05) after 13years. The three trials with poor-quality data do not provide reliable estimates of the effects on mortality (seeMethodological quality above). The available data showed RR=0.99 (0.95–1.02) after seven years andRR=1.01 (0.98–1.04) after 13 years; there was heterogeneity after seven years (p=0.07).

Deaths ascribed to breast cancer (graphs, outcomes 8-13)

Breast cancer mortality was unreliable and biased in favour of screening (see Methodological quality andDiscussion), but is included because it was the main outcome in all trials.

The two trials with medium-quality data failed to find an effect of screening on deaths ascribed to breastcancer (RR=1.05, 0.83–1.33) after seven years and (RR=0.97, 0.82–1.14) after 13 years. The three trials withpoor-quality data found a marked effect, RR=0.74 (0.61–0.90) after seven years and RR=0.68 (0.58–0.78)after 13 years. The difference between the two effect estimates is significant, both after seven years (z=2.29,p=0.02) and after 13 years (z=3.20, p=0.001). Because of this heterogeneity, and the methodologicaldifferences between the trials, it would be inappropriate to pool the data from all five trials.

There was no significant effect of screening on deaths ascribed to breast cancer among younger women(RR=1.33, 0.92–1.92) after seven years and (RR=1.03, 0.77–1.38) after 13 years for the trials with medium-quality data. Young women were under 50 years of age at randomisation in all analyses except for Malmöafter seven years, for which the limit was 55 years. For older women, the estimates for the trials withmedium-quality data were also non-significant (RR=0.88, 0.64–1.20 and RR=0.94, 0.77–1.15, respectively).

Deaths ascribed to any cancer (graph, outcome 14)

The two trials with medium-quality data failed to find an effect of screening on deaths ascribed to any cancer,including breast cancer (RR=1.02, 0.95–1.10; 10.5 years of follow-up for Canada, nine years for Malmö).


Heterogeneity was present (p=0.10); a random-effects model gave RR=1.03 (0.92–1.15). The estimate for thetrials with poor-quality data was similar (RR=1.00, 0.91–1.10).

Mastectomies and tumourectomies (graphs, outcomes 15 and 16)

The total number of mastectomies and tumourectomies was significantly higher in the screened group(RR=1.31, 1.22–1.42 for the trials with medium-quality data and RR=1.38, 1.21–1.58 for the trials with poor-quality data). As the mean follow-up was seven years for Canada and nine years for Malmö, this surgerydifference was not only an initial phenomenon, caused by the tumours detected at the prevalence screen, butseemed to persist. For Stockholm, we found data pertaining to the first round of screening only (RR=1.37,1.04–1.79).

The total number of mastectomies (excluding partial mastectomies, quadrantectomies and tumourectomies)was significantly higher in the screened group (RR=1.20, 1.08–1.32 for the trials with medium-quality dataand RR=1.17, 1.01–1.35 for the trials with poor-quality data).

Radiotherapy (graph, outcomes 17)

The number of women who received radiotherapy was significantly higher in the screened groups (RR=1.24,1.04–1.49 for Malmö, RR=1.40, 1.17–1.69 for Kopparberg before screening in the control group started).

Other adjuvant therapy (graphs, outcomes 18 and 19)

We found little information on other adjuvant therapy (see graphs), but it differed substantially in twocontemporaneous Swedish trials. Chemotherapy was given to only 7% of the breast cancer patients in Malmöbut to 31% in Kopparberg before the control group was screened. Conversely, hormone therapy was given to17% in Malmö, and to 2% in Kopparberg. Information exists from this trial on therapeutic adjuvant therapygiven over the years but the authors have not reported it (45).

Adverse effects

We found no data in the trial reports on psychological morbidity measured both in the screened group and inthe control group. Duration of sick leave and mobility of the shoulder were registered in the Two-Countystudy (38) but seem not to have been reported.

DiscussionThe main outcome measure in the screening trials was breast cancer mortality. This seems rational, as largertrials would be needed to show an effect on overall mortality. However, it is little realised that the tacitassumption that a demonstrated effect on breast cancer mortality can be translated into improved overallsurvival rests on pretty strong premises that may not be correct. Assessment of cause of death is fraught withdifficulties, and if this process is biased, breast cancer mortality may be misleading. Another importantproblem is that screening may lead to an increase in mortality from other causes.

We found no reliable evidence that mammographic screening reduces overall mortality. Our relative riskestimate, 1.00 (0.96–1.05), for the trials with medium-quality data from Canada and Malmö is in closeagreement with the less reliable, updated result for the Swedish trials, which was 1.00 (0.98–1.02) afteradjustment for imbalances in age (29). If the true effect of screening is a 30% reduction in breast cancermortality, as has been claimed, at least a 1% reduction in overall mortality would be expected, correspondingto a relative risk of 0.99. The trials were not powered to detect a beneficial or harmful effect on overallmortality but we find it discouraging that there was not even a tendency to a decline in mortality.

The two trials with medium-quality data did not find a reduction in breast cancer mortality, in contrast to theresults of the trials with poor-quality data (Göteborg, Stockholm and Two-County). We will try to explain thelikely reasons for this discrepancy.

Methodological limitations of the trials

Complex designs and insufficient reporting precluded us from providing reliable estimates for all-causemortality in the trials with poor-quality data. Our results for breast cancer mortality agreed with those


reported by the authors, but breast cancer mortality is not a reliable outcome (see below). As we haveindicated (Methodological quality), it is unlikely that the New York trial found a true reduction in breastcancer mortality. The brief report of the Malmö MMST II trial (55), which involved 25 770 women aged45–49, describes a large, significant effect on breast cancer mortality (RR=0.64, 0.45–0.89) which issurprising, since all meta-analyses which have taken trial quality into account have failed to find an effect inwomen under 50 years of age.

We find it disturbing that the largest effects on breast cancer mortality were reported in trials that had longintervals between screenings (Two-County trial), that invited a large fraction of the women to only two orthree screenings (Two-County and Stockholm trials), that started systematic screening of the control groupafter three to five years (Two-County trial, Göteborg trial and Stockholm trial) and that had poor equipmentfor mammography (New York trial). This is contrary to what one would expect and suggests that differencesin reported effects between the trials are related to the methodological quality of the trials and not to thequality of the mammograms or the screening programs.

We discussed above (see Methodological quality) that the finding of more small, node-positive cancers in thescreened group than in the control group in the Canadian trial cannot be used to judge the reliability of therandomisation process, because variables that become apparent as a result of the screening process arebiased. Whether a woman with a physical "abnormality" is referred for subsequent diagnosis (and biopsy) isinfluenced by the availability of mammograms in the screened group and their nonavailability in the controlgroup. Some women with four or more nodes were probably unrecognized in the control group, and manywere not even recognized subsequently, as their cancers spread, and they were more likely to be treated incentres where careful extensive nodal dissection was not the norm (92). The Canadian trial has beencriticised for including examination of the breasts in the control group among women under 50 years of age.However, large randomised trials have failed to detect an effect of self-examination (93,94). If the Canadiantrial is ignored for this and other doubtful reasons, as it often has been, it does not change the conclusion thatthere is no reliable evidence that mass screening with mammography does more good than harm.

Previous meta-analysts have generally not heeded the methodological quality of the trials but have includedthem all, sometimes omitting the Canadian trial and sometimes even including case-control studies (28).Those who regarded quality issues (15,18) have tended to rate the Canadian trial as of high quality and theTwo-County trial as of poor quality, in one case blindly (18). Trials with inadequate or unclearly describedrandomisation methods exaggerate the estimated treatment effect by 30–40% on average (95-97), and wefound differences of this magnitude between our effect estimates for breast cancer mortality between themedium-quality trials and the poor-quality trials.

Control group women in the trials received usual care whereas women in the screened group, in particularthose with screen-detected cancers, would be more likely to be treated in specific centres (92). This couldhave resulted in better management and treatment, but there was not enough information in the trial reports toreveal any bias.

An important problem relates to timing. Entry dates into the trial were defined differently for women in thescreened and control groups in several of the trials. This casts further doubt on the quality of therandomisation process.

Misclassification of cause of death

The New York study shows how easily bias may creep in, even when cause of death is determined blindly.Since the numbers of tumours identified were very similar in the screened group and the control groupthroughout this study (40,49,83) and, accordingly, the number of dubious cases selected for review was alsovery similar, the probability that a dubious cause of death would be labelled a breast cancer death afterblinded review would be expected to be the same. As noted above, however, directly observable differentialmisclassification might be responsible for approximately half of the reported breast cancer mortality benefit.

The importance of autopsy is illustrated by the fact that many of these women have two or three types ofcancer (54). Of 193 women with breast cancer who died in the Malmö trial, 41 (21%) had or had previously


had at least one other malignancy (98). The authors noted that "many of the breast cancer victims suffer notfrom breast cancer but from cancer disease". Patients with cachexia and other signs of progressive neoplasiaand no signs of recurrence of breast cancer would likely be assigned to another type of cancer. It isnoteworthy that mortality for any cancer was very similar in the screened groups as in the control groups.

We found data from the Two-County trial (86) that could illustrate this possible misclassification directly(graph no. 20). Among women with a diagnosis of breast cancer, mortality for other cancers was significantlyhigher (RR=2.42, 1.00–5.85) (p=0.05); mortality from all other causes was also higher, although notsignificantly (RR=1.37, 0.93–2.04) (p=0.11). It could be argued that only those women who did not die frombreast cancer should appear in the denominators but this procedure would tend to obscure anymisclassification, because the denominators in the control groups were much smaller than those in the studygroups. This calculation gives RR=2.23 (0.93–5.39) and RR=1.27 (0.86–1.87), (p=0.07 and p=0.24,respectively), which still suggests misclassification. The increase in mortality for causes other than breastcancer amounts to 38% of the reported decrease in breast cancer mortality in the Kopparberg part of the trialand 56% in the Östergötland part. Differences in age could not be the explanation, because age at diagnosisof breast cancer was very similar for the study and control groups in the trials. In Malmö, those mean ageswere 62.15 years in the study group and 61.91 years in the control group (4), in New York, they were 54.9and 54.5 years (1) and in Stockholm, the age was 61.7 years with no significant difference between study andcontrol groups (60). One would therefore have expected similar mortality rates from other cancers and fromall causes.

The Two-County study is difficult to evaluate. Results are often presented in different ways and we founddiscrepancies in numbers of women and deaths, even sometimes within the same article. For example, in theage group 40–49 years, 26 vs 18 deaths from breast cancer were reported for Kopparberg in 1993 (85,99)which changed to 22 vs 16 in 1996 (62,100), to 23 vs 18 in 1997 (26) and back again to 26 vs 18 in 1999(101). For Östergötland, these numbers were 24 vs 19, 23 vs 23, 27 vs 27 (26) and 28 vs 28, respectively, i.e.after the blinded endpoint committee had done its work in 1993, a more favourable result for screening, withboth fewer and more deaths was reported.

In the Malmö study - as originally published in 1988, when the autopsy rate for breast cancer cases was ashigh as 76% - the relative risk of dying for the screened group was 0.96 for breast cancer deaths, for othercancer deaths (among all randomised women) and for any cancer. In contrast, in the Two-County study, inwhich the autopsy rate was only 36% (65), the relative risks after seven years were 0.71, 1.05 and 1.00,respectively. Thus, the apparent benefit for breast cancer mortality disappeared when the outcome wasmortality from any cancer. This can hardly be attributed to the fact that the study group women in the Two-County trial were slightly older than those in the control group, since the relative risk for overall mortalityafter seven years was 1.01 for the Two-County trial without adjustment for age (65).

The autopsy rates in the Göteborg and Stockholm trials were 31% and 22%, respectively (29). The updatednumbers of breast cancer deaths in Malmö seem to be less reliable than the originally reported ones, as theautopsy rate was halved from 1985 to 1997 (Andersson, personal communication, 10 Oct 2000). We includedthis update, which was more favourable to screening than the original data, in our meta-analysis of follow-upafter 13 years. Causes of deaths were reclassified in some patients in conjunction with the update of theSwedish trials (11). As in the New York study, the outcome of the blinded reclassification process favouredthe screened groups. Breast cancer was considered the underlying cause of death in 419 of the screenedgroup and 409 of the control group according to Statistics Sweden and in 418 and 425 cases, respectively,according to the committee (102). The 17 net reclassifications favoured the screened group, and since therewas disagreement as to cause of death for only 89 patients, this suggests bias. Suzanne Fletcher has called fornumerical reporting, for each study, of the results and changes in classification (99), but as far as we know,this has not been done.

Several commentators have suspected that misclassification of cause of death might have occurred in some ofthe trials (91,99,103,104). Misclassification bias is difficult to avoid, even with the best of intentions: forexample, using a blinded endpoint committee (11). Radiotherapy, for example, reduces the rates of local


recurrence by about two-thirds (34). Early cancers are treated by tumourectomy and radiotherapy, whichmight increase the likelihood that deaths among screen-detected breast cancer cases will be misclassified asdeaths from other causes (33) and that too many deaths in the control group will be misclassified as breastcancer deaths, particularly among women who are not autopsied. For example, the Swedish trials stated that"most patients with locally advanced disease will die due to cancer" and that breast cancer as the underlyingcause of death includes women with locally advanced breast cancer, whereas women who have been treatedsuccessfully should not be classified as having breast cancer deaths if another specified disease could be thecause of death (29).

Belief in the effectiveness of an intervention may influence quite substantially the decision on which type ofcancer caused the patient's death. A carefully conducted study showed that prostate cancer patients who didnot die from prostate cancer had a proportionate mortality for other causes, which was very similar to acohort of patients with benign prostatic hyperplasia (105). However, those with no initial treatment had aproportionate mortality for other cancer causes of 13.7%, significantly lower (p=0.019) than the 18.9% seenin the non-prostate cancer cohort. Conversely, the cancer proportionate mortality in the aggressively treatedsubgroup was 29.9%, significantly higher (p<0.001) than that in the non-prostate cancer cohort. Thisindicates that if it is believed that an intervention is successful, there is a tendency to put some other cause ofdeath on the death certificate.

These data suggest that proving the correctness of cancer-specific mortality rates is impossible. Also,complications of cancer treatment cause mortality that is often ascribed to other causes. The size of thismisclassification is 37% for cancer generally and 9% for breast cancer (106). Finally, as women with breastcancer are about 60 years of age at diagnosis on average, death of such patients may represent theculmination of other medical problems which, again, opens the door to bias.

Screening-associated increase in mortality

Radiotherapy reduces annual mortality rates from early breast cancer by 13.2% but increases those fromother causes by 21.2% (34). It can be predicted that overall, radiotherapy is beneficial for women at high riskof local recurrence, but harmful for women at low risk, such as those identified by screening, primarilybecause of an excess of cardiovascular deaths (34). The adverse effect may be apparent early, and mayexplain why overall mortality at seven years appeared higher among women aged 40–49 in the screenedgroup in Kopparberg (RR=1.33, 1.02–1.74), where radiotherapy was used extensively. This finding was notmentioned by the authors but can be calculated by adding numbers from two tables (63). For the women inthe screening groups in the Swedish trials (21), a non-significant tendency to an increase in mortality fromcardiovascular diseases was reported after adjustment for the age imbalances (RR=1.02, 0.98–1.06). This iswhat one would expect (because most women who die from cardiovascular diseases do not have breastcancer, one would only expect to see a tendency, and not a significantly harmful effect). The investigatorsreported data for two subgroups as well, ischaemic heart disease (RR=1.00) and cerebrovascular diseases(RR=1.04). The "rest group" of cardiovascular diseases not reported on is important, as it included heartfailure, for example. Based on a weighted average we calculated RR=1.05 for this subgroup (adjusted for theage imbalances).

The Swedish trials (apart from Malmö) were contaminated by early introduction of systematic screening inthe control group (29,102) and have been criticised for this previously (99). That early contamination of thecontrol group would preclude long-term evaluation of the effect on all-cause mortality was pointed out beforethe start of the Two-County trial (39). Shortly before the control group screening started it was agreed at aninternational meeting of investigators that the randomised design should be kept as long as possible to allowan evaluation of the effect of screening (53). In 1999, the Two-County trial, which was the first to introducescreening in the control group, was criticised by the Swedish Medical Research Council and the SwedishCouncil for Technology Assessment in Health Care in relation to this problem (68). It has been argued thatscreening the controls would lead to an underestimate of the benefit of screening for breast cancer mortality.However, it may also lead to an underestimate of the harmful effect of screening. Screening the control groupwould be expected to increase mortality from causes other than breast cancer by subsequent use of


radiotherapy. It therefore tends to obscure this detrimental effect, the full consequences of which we stillhaven't seen since it persists for more than two decades (34). An additional bias favouring screening iscaused by the fact that the control group was screened later than the last screening in the study group(10,107), which led to, for example, 21% more invasive carcinomas detected per woman in the control groupthan in the screened group in Göteborg (10).

Proponents of screening programs have generally disregarded their adverse effects, even when the possibilityof an increase in overall mortality was raised (30-32,65). The project group for the Two-County study andthe Swedish National Board of Health, which initiated and sponsored the study, reassured a critic (30) thattotal mortality was irrelevant and without scientific basis, and that they considered it an absurd thought thatscreening with mammography could have increased mortality in the study group (65). When the meta-analysis of the Swedish trials was published (11), two correspondents (31,32) commented on the increase inoverall mortality in the study groups and one called for a direct comparison of the mortality rates in theexposed and control groups. In reply, however, only indirect comparisons with population data wereprovided (85).

The Swedish trialists have recently admitted that "the total cumulative mortality would seem to be the mostobjective measure" (20). Long-term overall mortality can be evaluated most reliably for the Canadian trial,because the other trials were contaminated or had differentially excluded some of the women afterrandomisation. Relative risk in the screened group after 13 years was 1.04 (0.96–1.13). If the Malmö trial isadded, RR=1.00 (0.96–1.05). In a worst-case scenario where the 154 and 45 excluded women had all died,the RRs for overall mortality become 1.04 (0.98–1.10) after seven years and 1.03 (0.98–1.07) after 13 years.

Does screening lead to less aggressive treatment?

It is often asserted that early detection spares patients more aggressive treatments, in particular mastectomy(22,63,108-110). However, because of overdiagnosis (2,56,111,112), one would expect more rather than lesssurgery of all kinds. We found that screening increased the number of mastectomies by about 20% and thenumber of mastectomies and tumourectomies by about 30%. In Kopparberg, an additional 97 operationswere performed when the control group was screened. If these data are included, the RR for breast surgeryfor the screened group in Kopparberg changes from 1.39 (1.19–1.62) to 0.96 (0.84–1.10). This illustrates thatdata on harms are unreliable after screening has been introduced in the control group.

This documented increase in aggressive treatment is in contrast to the assertions to the contrary by sometrialists despite their access to the necessary data (63), and in contrast to publications that base their claims onrelative numbers rather than absolute numbers (110). In the latter case, the proportion of breast preservingoperations is said to be increasing, but the trend for the number of mastectomies is not revealed.

The increased mastectomy rate could be speculated to be somewhat overestimated since there has been ageneral policy change towards less mastectomies. However, this is probably not the case as average age atdiagnosis was the same in the screened and control groups. Furthermore, there was a similar increase inmastectomies in Stockholm, where the data pertains to the first round only, as in Malmö and Canada afterlong-term follow-up. In fact, it is more likely that the increase is an underestimate as re-operations andoperations in the contralateral breast seemed not to have been included.

In 1985, there was a discrepancy between the rates of mastectomy and breast cancer in the UK whichindicated overdiagnosis (113). In the USA, where mammography has been aggressively marketed, 10 242cases of carcinoma in situ were treated by mastectomy in 1992 (114), and the rate of mastectomy was abouttwice as high as in Britain in the late 1970s, although the incidence of breast cancer was similar (103). Anadditional problem is that up to 50% of lesions detected by mammography will be nonpalpable, and ascytological diagnosis may be less reliable in these cases, open surgery biopsy is used frequently (115).Operations for such lesions are often more difficult and traumatic than those for a palpable lesion and theresults can be unsightly (116).

Quality assurance programs could possibly reduce the harmful effects of screening to some degree but theycannot be avoided. Screening not only identifies slow-growing tumours, but it also identifies cell changes


which are histologically cancer but biologically benign (2,111). The survival rate for screening-detectedcancers is therefore extremely high, for example, 97% in Malmö after 10 years follow-up (98). It is evenhigher than for cancers in the same stage detected clinically (117). Carcinoma in situ is particularlyproblematic. Because more ductal carcinoma in situ lesions are detected in the screened groups (for example,123 vs 20 before controls were screened in the Two-County trial (118), re-operations and bilateral operationsshould be more common among screened women. In Kopparberg, the number of operations for breast cancerdoubled during the prevalence screen and remained about 75% higher also in the following years (115). Inhalf of the patients with carcinoma in situ, the extent of the lesions is 5 cm or more, so most lesions havetherefore been treated by mastectomy, which is often bilateral, as lesions may be found in the other breast inabout 40–50% of the women (119). There seems to be comparatively more carcinoma in situ in youngwomen (9) who would then have to live many years in uncertainty.

It is sometimes argued that since mammographic methods have improved, the benefit of screening should belarger than shown in the screening trials. However, the sensitivity in the studies that followed the New Yorktrial has not consistently improved (99), and meta-analyses have failed to find any association betweenmammographic quality and breast cancer mortality (17,18). Furthermore, “better “ diagnostic methods mighteven lead to additional overtreatment. Breast cancer malignancy was found in 22 of 110 consecutivemedicolegal autopsies of women with a median age of 39 years; 20 were carcinoma in situ lesions (120). Thechance that in situ cancer does not develop into invasive cancer seems to be about 70–75% (120). Thus,many cell changes that would never have developed into cancer in the women's lifetime, may, in the presenceof a screening program, be treated by mastectomy or large local resection plus radiotherapy (121).

False-positive diagnoses, psychological distress and pain

In an American cohort of 2400 women, 40–69 years of age, a median of four mammograms per screenedwoman were performed, and 23.8% had at least one false positive mammogram during 10 years (122). Theestimated cumulative risk of a false-positive result after 10 mammograms was 49.1%. An estimated 18.6%will have undergone a biopsy. The percentage of false-positive screening mammograms increased from 4.2%to 7.6% in a seven-year period. These estimates would be expected to be lower in Europe, where the rate offalse-positive mammograms has usually been about 4% to 5% in the first round and less thereafter(55,123,125).

A systematic review has shown that the psychological distress caused by false-positive diagnoses cannot beignored (126). In the Stockholm trial, 64% and 73% of women with false-positive findings in the first andsecond screening rounds were declared cancer-free at six months (9). Three months after they had false-positive results, 47% of women who had highly suspicious readings reported that they had substantial anxietyrelated to the mammogram, 41% had worries about breast cancer, 26% reported that the worry affected theirdaily mood, and 17% that it affected their daily function (compared to 3% with a normal mammogram)(126). In Norway, 18 months after screening mammography, 29% of women with false-positive results and13% of women with negative results reported anxiety about breast cancer (127).

Thus, it can be estimated that screening inflicts important psychological distress for many months on morethan a tenth of the healthy population of women who attend a screening program, but women invited forscreening have not been informed about this risk (128,129) and the risk of receiving the diagnosis ofcarcinoma in situ (130). Finally, a substantial proportion of women experience pain related to mammography(131).

Costs

Information on total costs was not reported for any of the trials. The costs associated with running nationalscreening programs are high. The National Health Service in UK has never invested more in implementing anew type of clinical practice (132) and the annual cost of the Swedish program has been estimated to beabout 500 mio sw.kr. (133). The decision to embark on the UK screening program was made mainly becauseof the positive results in the New York and Two-County trials (12). It is not surprising that policy makers andmany scientists have believed that the benefit of screening was well documented. Essential information for


judging the reliability of the trials was often unpublished or published only in Swedish, in theses, letters,conference reports, reviews, or in journals that are not widely read, and with titles and abstracts that did notindicate that important information was to be found. It has recently been suggested that resources beredirected to interventions with proven benefit in breast cancer (134).

Reviewers' conclusionsImplications for practice

The currently available reliable evidence has not shown a survival benefit of mass screening for breastcancer. However, the trials and this review are still underpowered for all-cause mortality; the confidenceintervals include both a plausible worthwhile and a possible detrimental effect. Mass screening leads tooverdiagnosis and increased use of more aggressive treatment. Women, clinicians and policy makers shouldconsider these findings carefully when they decide whether or not to attend or support screening programs.

Implications for research

Breast cancer mortality is an unreliable outcome measure in screening trials (and therefore also in cohortstudies of the effectiveness of national programs). Hence, an effect on overall mortality needs to be shown inhigh-quality randomised trials before a decision can be reached whether or not a screening program forcancer is worthwhile. There are also ethical reasons, as mass screening involves the entire population andmay cause a screening-associated increase in mortality as well as other harm. Whether screening for breastcancer is beneficial in terms of overall mortality among women at higher risk (for example, women withmore than one first-degree relative with breast cancer, and elderly women) could be investigated. Such trialsare feasible. Based on the 1993 meta-analysis of the Swedish trials (11,31), in which breast cancer mortalitywithout screening constituted only 3.5% of the total mortality because large numbers of women with breastcancer were excluded from the trials, it can be calculated that to detect a decrease in overall mortality from10.33% to 10.22% (RR=0.989), which corresponds to a decrease in breast cancer mortality of 30%, with typeI and type II errors of 5% and 20%, respectively, a trial with 1.2 million women in each arm would beneeded. A trial in women at higher risk could be much smaller.

AcknowledgmentsWe wish to thank Freda Alexander, Ingvar Andersson, Cornelia Baines, Niels Bjurstam, Gunnar Fagerberg,Jan Frisell, Anthony B. Miller and Sam Shapiro for helpful comments on their trials. Thanks also to MikeClarke.

Potential conflict of interestNone. We had no a priori opinion on the effect of screening for breast cancer when we were asked in 1999 bythe Danish Institute for Health Technology Assessment, the National Board of Health, to review therandomised trials.

Another, less comprehensive version of this review will be published in The Cochrane Library on October22, 2001: Olsen O, Gøtzsche PC. Screening for breast cancer with mammography (Cochrane Review). In:The Cochrane Library, Issue 4, 2001. Oxford: Update Software.

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Table 1. Characteristics of included studies

Study Methods Participants Interventions Outcomes Notes

Canada1980

Individualrandomisation inblocks of 2 or 4,stratified by centreand 5-year agegroup (see alsotext).

Cause of death wasassessed blindedand independentlyby two specialistsfor women withdiagnosed breastcancer and for otherpossible breastcancer deaths.

Women aged40-59.

Two-viewmammographycranio-caudal andmediolateral (latermedio-lateraloblique except intwo centres).

4-5 cycles ofscreening withyearly interval.

Totalmortalitybreastcancermortalitysurgicalinterventions

Attendance rate:100% in firstround.

Mammographyin control group:Screening ofhigh risk groupsnot precluded.

(see also Canada1980a and1980b)

Canada1980a

See Canada 1980.

Women aged40-49.

50,472randomised.

42,distributedequallybetween thetwo groups,

See Canada 1980.

Screened womenhad an annualclinicalexamination whilecontrol womenwere examined atthe first visit andwere taught self-examination

SeeCanada1980.

Attendance rate:100% in firstround, 89% insecond,decreasing to86% in fifthround.

Mammographyin control group:7% between first


wereexcludedfromanalyses.

thereafter. and second year,increasing to18% betweenfourth and fifthyear had amammogram.

Canada1980b

See Canada 1980.

Women aged50-59.

39,459randomised.

54,distributedequallybetween thetwo groups,wereexcludedfromanalyses.

See Canada 1980.

All women hadtheir breastsexamined annually.

SeeCanada1980.

Attendance rate:100% in firstround, 90% insecond,decreasing to87% in fifthround.

Mammographyin control group:5% between firstand second year,increasing to 8%between fourthand fifth yearhad amammogram.

Edinburgh1978

Stratified clusterrandomisation;general practiceswere clusters;stratification wasby size of practice.About 87 clusters(numbers vary indifferent reports,see also text).

Blinding ofoutcomeassessment notstated.

Women aged45-64.

Number ofwomen andpracticesrandomisedinconsistentlyreported (seetext).

Very biasedexclusionsoccurred:exclusionproceduresdifferent instudy andcontrol group,177 previous

Two-viewmammography atfirst screen: cranio-caudal and oblique(except in onepractice); onlyoblique in laterrounds.

Screened group:mammography andphysicalexamination year 1,3, 5 and 7; physicalexamination year 2,4 and 6.

Control group:usual care.

Totalmortalitybreastcancermortalityradiotherapy

Attendance rate:Ca. 60 % in firstround; 44% inseventh round.

Mammographyin control group:unknown.


breast cancercasesexcludedfrom controlgroup and338 fromstudy group.

Göteborg1982a

Individualrandomisationwithin year of birthcohort - by day ofbirth in the cohorts1923-35 and bycomputer softwarefor the cohorts1936-44 -randomisation ratioapproximately 1:1.2(see also text).

Blinding ofoutcomeassessment notstated but done forbreast cancer casesin conjunction withSwedish meta-analysis.

Women aged39-49.

Number ofwomenrandomised:11792 toscreening,14321 tocontrol (seealso text).

68 women(0.6%)excludedfrom thescreeninggroup and104 (0.7%)from thecontrol groupdue to ahistory ofbreastcarcinomaprior torandomisation.

Two-viewmammography atfirst screen, singleat later rounds -single read at firstthree rounds;double readthereafter.

5 cycles with aninterval of 18months.


Totalmortalitybreastcancermortality

Attendance rate:85%, 78%, 79%,77%, 75% inrounds 1-5.66% at firstscreen in controlgroup.

Mammographyin control group:19% during lasttwo years; 51%ever.

Early systematicscreening ofcontrol group.

Göteborg1982b

Individualrandomisation bycomputer software -randomisation ratio1:1.6.Blinding ofoutcomeassessment: See

Women aged50-59.Number ofwomenrandomisednot statedexplicitly."W

Trial has not beenfully reported.

Trial hasnot beenfullyreported.

Trial has notbeen fullyreported.Earlysystematicscreening ofcontrol group.


Göteborg 1982a. omen with ahistory ofbreastcarcinomaprior torandomization wereidentified andexcludedfrom theanalysis,although notfrom the trialprocedure"but nonumbersgiven.

Kopparberg 1977

Stratified clusterrandomisation;seven blocks eachcontained 3 units(in three blocks theunits were parishesand in fourmunicipalities);randomisation ratio2:1 (see also text).


Women aged40 and above.

21 unitsrandomised:47389 womenin screeningareas and22,658 incontrol areas(33,641 vs.16,359 in agegroup 40-69;39,051 vs.18,846 in agegroup 40-74).

No parishesormunicipalitiesexcluded.Exclusioncriteria forpatientsunclear butprobably

One-viewmammography,mediolateraloblique; additionalviews on suspicion.

Number ofscreenings: twocycles pre-stated,but more may haveoccured (see text).Interval betweenscreens were 2years for womenaged 40-49;3 years for womenaged 50 and above.

Totalmortalitybreastcancermortalitysurgicalinterventionschemotherapyradiotherapy

Attendance rate:91-94% forwomen youngerthan 60 years;50-80% forwomen above 60years.

Unclear whenscreening startedin control group(see text).



biased (seetext).

Malmö1976

Individualrandomisation;within each birthcohort a computerlist was randomisedand the first halfinvited forscreening.

Blinding ofoutcomeassessment: deathsamong breastcancer casesassessed blindedand independentlyby a pathologist andan oncologist;discrepanciesresolved by aninternist.

Women aged45-69.

21,242randomisedinto screenedgroup; 21,240or 21,244 intocontrol group(see text).

Biasedexclusionsseem to haveoccurred: 154womenexcludedfrom controlgroup49 from studygroup (seetext).

One-view or two-viewmammography;two-view in 1st and2nd round; one-view or two-view inlater roundsdepending onparenchymalpattern.

5-6 cyclesaccording toprotocol; 8 cyclesin 1988; moreduring 1988-1992.

Interval betweenscreens: 18-24months.


Totalmortalitybreastcancermortalitysurgicalinterventionschemotherapyradiotherapy

Attendance rate:Cirka 70%; 74%in first roundranging from64% in oldestage group to79% inyoungest.

Mammographyin control group:screeningoffered to agegroup 50-69 in1991; invited in1992 andcompleted in1993.

6% had morethan 3mammogramsduring study ;24% had one ormore; 35%among womenaged 45-49 atentry.

New York1963

Individualrandomisationwithin matchedpairs; pairs derivedfrom a computerlist sorted by age,family size andemployment group.

A blinded reviewwas carried out in asubsample of deathcertificates where

Women aged40-64.

Probably31,092 pairsof womenwererandomisedinto screeningand controlgroup.

Very biasedexclusions

Two viewmammography:cephalocaudal andlateral.4 cycles (three wereplanned accordingto the firstpublications).

Screened group:annual physicalexaminations.

Control group:

Totalmortalitybreastcancermortalitysurgicalinterventionsradiotherapy

Attendance rate:65% in totalpopulation, ca.58%, 50% and40% participatedin 2, 3 and 4screens,respectively.

Mammographyin control group:not described.


cause of death wasbreast cancer. Thepanel much moreoften stated breastcancer as cause ofdeath in the controlgroup.

occurred:probably 336previousbreast cancercases wereexcludedfrom thecontrol groupand 853 fromstudy group(see text).

usual care.

Stockholm1981

Individualrandomisation byday of birth; 1-10and 21-31 in studygroup and 11-20 incontrol group (seealso text).

Blinding ofoutcomeassessment:not stated.

Women aged40-64.

Number ofwomenrandomisedinconsistentlyreported (seetext).

Exclusionsafterrandomisation unclear (seetext).

Single obliquemammography;recalled forconventional three-view ifmalignanciessuspected.

2 cycles (numbernot predetermined -screeningintroduced incontrol groupbecause of resultsfrom Kopparberg).

Ca. 2 years; 2.5years to completefirst round and 2.1to complete secondround.


Totalmortalitybreastcancermortalitysurgicalinterventions

Attendance rate:ca. 80%.

Mammographyin control group:8% during oneyear; 25% instudy groupduring threeyears previous toscreening.


Two-county1977

Stratified clusterrandomisation (seeKopparberg 1977and Östergötland1978 for details).

Blinding of causeof deathassessments in

Women aged40-74.

(SeeKopparberg1977 andÖstergötland1978 for

See Kopparberg1977 andÖstergötland 1978.

Screened womenwere encouraged toperform self-examination of thebreasts every

SeeKopparberg 1977 andÖstergötland 1978.

See Kopparberg1977 andÖstergötland1978.


some later updates. details). month.

Control women:usual care.

Östergötland 1978

Stratified clusterrandomisation; 12blocks (consistingof 164 parishes intotal) were eachsplit into 2 units ofroughly equal sizeand socio-economiccomposition;randomisation ratio1:1 (see also text).


Women aged40 and above.

24 units with92934womenrandomisedinto 47001 inscreeningparishes and45933 incontrolparishes(39034 vs.37936 in agegroup 40-74).

No parishesormunicipalitiesexcluded.

Women witha previoushistory ofbreast cancerwereexcluded afterrandomisation; exclusionsseemunbiased (seetext).

One-viewmammography,mediolateraloblique; womenwho reported alump wereexamined clinicallyand by completemammography.

2 screens forwomen above 70years, 3 for womenoriginally in agegroup 40-69.

Interval betweenscreens: 2-2.5years.

Totalmortalitybreastcancermortality .

Attendance rate:ca. 90% in firstround,80% in second,very agedependent.

Mammographyin control group:no data.


Table 2. Summary of the methodological quality of the trials. Yes: criterion met, No:criterion not met, ?: uncertain.


StudyRandomisationadequate

Baselinecomparability

No importantexclusions

No earlycontamination

Mortality datareliable

Canada 1980 Yes Yes Yes Yes Yes

Edinburgh 1978 No No No Yes No

Göteborg 1982a ? ? ? No No

Malmö 1976 Yes ? No Yes ?

New York 1963 Yes No No Yes No

Stockholm 1981 No ? ? No No

Two-County 1977 No ? No No No

Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 02 Overall mortality, 7 years follow-up

Study Screening No screening RR (fixed) Weight RR (fixed)or sub-category n / N n / N 95% CI % 95% CI

01 Medium quality data Malmö 1976 1777 / 21088 1809 / 21195 81.63 0.99 [0.93, 1.05] Canada 1980a 159 / 25214 156 / 25216 7.06 1.02 [0.82, 1.27] Canada 1980b 253 / 19711 250 / 19694 11.31 1.01 [0.85, 1.20] Subtotal (95% CI) 2189 / 66013 2215 / 66105 100.00 0.99 [0.94, 1.05]Test for heterogeneity: Chi? = 0.13, df = 2 (P = 0.94)Test for overall effect: Z = 0.27 (P = 0.79)

02 Poor quality data Kopparberg 1977 2593 / 39051 1216 / 18846 28.04 1.03 [0.96, 1.10] Östergötland 1978 2253 / 39034 2204 / 37936 38.21 0.99 [0.94, 1.05]

Stockholm 1981 1768 / 39139 1036 / 20978 23.06 0.91 [0.85, 0.99] Göteborg 1982a 178 / 10888 185 / 13203 2.86 1.17 [0.95, 1.43] Göteborg 1982b 349 / 10112 591 / 15997 7.83 0.93 [0.82, 1.06] Subtotal (95% CI) 7141 / 138224 5232 / 106960 100.00 0.99 [0.95, 1.02]Test for heterogeneity: Chi? = 8.82, df = 4 (P = 0.07)Test for overall effect: Z = 0.80 (P = 0.42)

0.5 0.7 1 1.5 2

Favours screening Favours no screening

Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 03 Overall mortality, 13 years follow-up


01 Medium quality data Malmö 1976 2537 / 21088 2593 / 21195 70.08 0.98 [0.93, 1.04]

Canada 1980a 418 / 25214 414 / 25216 11.22 1.01 [0.88, 1.16] Canada 1980b 734 / 19711 690 / 19694 18.70 1.06 [0.96, 1.18] Subtotal (95% CI) 3689 / 66013 3697 / 66105 100.00 1.00 [0.96, 1.05]

Test for heterogeneity: Chi? = 1.80, df = 2 (P = 0.41)Test for overall effect: Z = 0.05 (P = 0.96)


Göteborg 1982a 409 / 11724 506 / 14217 5.08 0.98 [0.86, 1.11]

Subtotal (95% CI) 11272 / 89234 7988 / 70371 100.00 1.01 [0.98, 1.04]Test for heterogeneity: Chi? = 1.89, df = 2 (P = 0.39)Test for overall effect: Z = 0.84 (P = 0.40)

0.5 0.7 1 1.5 2



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 04 Overall mortality, 7 years follow-up, younger women (below 50 years of age)


01 Medium quality data Canada 1980a 159 / 25214 156 / 25216 100.00 1.02 [0.82, 1.27] Subtotal (95% CI) 159 / 25214 156 / 25216 100.00 1.02 [0.82, 1.27]


02 Poor quality data Kopparberg 1977 188 / 9582 74 / 5031 13.70 1.33 [1.02, 1.74] Östergötland 1978 204 / 10262 227 / 10573 31.57 0.93 [0.77, 1.12] Stockholm 1981 274 / 14303 172 / 8021 31.12 0.89 [0.74, 1.08] Göteborg 1982a 178 / 10888 185 / 13203 23.61 1.17 [0.95, 1.43] Subtotal (95% CI) 844 / 45035 658 / 36828 100.00 1.03 [0.93, 1.14]Test for heterogeneity: Chi? = 8.47, df = 3 (P = 0.04)Test for overall effect: Z = 0.54 (P = 0.59)

0.5 0.7 1 1.5 2


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 05 Overall mortality, 7 years follow-up, elderly women (at least 50 years of age)


01 Medium quality data Canada 1980b 253 / 19711 250 / 19694 100.00 1.01 [0.85, 1.20] Subtotal (95% CI) 253 / 19711 250 / 19694 100.00 1.01 [0.85, 1.20]


02 Poor quality data Kopparberg 1977 3485 / 29007 1619 / 13551 30.58 1.01 [0.95, 1.06] Östergötland 1978 3385 / 28229 3332 / 26830 47.34 0.97 [0.92, 1.01] Stockholm 1981 1494 / 24836 864 / 12957 15.73 0.90 [0.83, 0.98] Göteborg 1982b 349 / 10112 591 / 15997 6.34 0.93 [0.82, 1.06] Subtotal (95% CI) 8713 / 92184 6406 / 69335 100.00 0.97 [0.94, 1.00]Test for heterogeneity: Chi? = 5.02, df = 3 (P = 0.17)Test for overall effect: Z = 2.19 (P = 0.03)

0.5 0.7 1 1.5 2


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 06 Overall mortality, 13 years follow-up, younger women (below 50 years of age)


01 Medium quality data Malmö 1976 176 / 3987 170 / 4067 28.90 1.06 [0.86, 1.30] Canada 1980a 418 / 25214 414 / 25216 71.10 1.01 [0.88, 1.16]


02 Poor quality data Kopparberg 1977 309 / 9650 137 / 5009 19.54 1.17 [0.96, 1.43] Östergötland 1978 265 / 10285 288 / 10459 30.93 0.94 [0.79, 1.10] Göteborg 1982a 409 / 11724 506 / 14217 49.54 0.98 [0.86, 1.11] Subtotal (95% CI) 983 / 31659 931 / 29685 100.00 1.00 [0.92, 1.10]Test for heterogeneity: Chi? = 3.15, df = 2 (P = 0.21)Test for overall effect: Z = 0.08 (P = 0.94)

0.5 0.7 1 1.5 2



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 07 Overall mortality, 13 years follow-up, elderly women (at least 50 years of age)



Canada 1980b 734 / 19711 690 / 19694 22.19 1.06 [0.96, 1.18]

Subtotal (95% CI) 3095 / 36812 3113 / 36822 100.00 1.00 [0.95, 1.04]


02 Poor quality data Kopparberg 1977 5725 / 28918 2659 / 13470 44.57 1.00 [0.96, 1.05]

Östergötland 1978 4564 / 28657 4398 / 27216 55.43 0.99 [0.95, 1.02]


0.5 0.7 1 1.5 2


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 08 Deaths ascribed to breast cancer, 7 years follow-up


01 Medium quality data Malmö 1976 63 / 21088 66 / 21195 49.55 0.96 [0.68, 1.35] Canada 1980a 38 / 25214 28 / 25216 21.08 1.36 [0.83, 2.21] Canada 1980b 38 / 19711 39 / 19694 29.37 0.97 [0.62, 1.52] Subtotal (95% CI) 139 / 66013 133 / 66105 100.00 1.05 [0.83, 1.33]Test for heterogeneity: Chi? = 1.44, df = 2 (P = 0.49)Test for overall effect: Z = 0.38 (P = 0.70)


Stockholm 1981 53 / 38525 40 / 20651 22.86 0.71 [0.47, 1.07]

Göteborg 1982a 6 / 10821 10 / 13101 3.97 0.73 [0.26, 2.00] Göteborg 1982b 21 / 9903 37 / 15708 12.56 0.90 [0.53, 1.54]

Subtotal (95% CI) 204 / 137334 206 / 106242 100.00 0.74 [0.61, 0.90]

Test for heterogeneity: Chi? = 1.00, df = 4 (P = 0.91)Test for overall effect: Z = 3.06 (P < 0.01)

0.2 0.5 1 2 5



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 09 Deaths ascribed to breast cancer, 13 years follow-up



Canada 1980a 82 / 25214 72 / 25216 25.28 1.14 [0.83, 1.56]

Canada 1980b 107 / 19711 105 / 19694 36.88 1.02 [0.78, 1.33]



Östergötland 1978 135 / 38491 173 / 37403 42.57 0.76 [0.61, 0.95] Stockholm 1981 66 / 40318 45 / 19943 14.61 0.73 [0.50, 1.06]

Göteborg 1982a 18 / 11724 40 / 14217 8.77 0.55 [0.31, 0.95]

Subtotal (95% CI) 345 / 129122 362 / 90145 100.00 0.68 [0.58, 0.78]Test for heterogeneity: Chi? = 2.95, df = 3 (P = 0.40)Test for overall effect: Z = 5.17 (P < 0.0001)

0.2 0.5 1 2 5


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 10 Deaths ascribed to breast cancer, 7 years follow-up, younger women (below 50 years of age; Malmö 55)



Canada 1980a 38 / 25214 28 / 25216 56.15 1.36 [0.83, 2.21] Subtotal (95% CI) 66 / 33195 50 / 33298 100.00 1.33 [0.92, 1.92]Test for heterogeneity: Chi? = 0.02, df = 1 (P = 0.89)Test for overall effect: Z = 1.51 (P = 0.13)



Göteborg 1982a 6 / 10821 10 / 13101 19.83 0.73 [0.26, 2.00]


0.2 0.5 1 2 5



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 11 Deaths ascribed to breast cancer, 7 years follow-up, elderly women (at least 50 years of age; Malmö 55)



Canada 1980b 38 / 19711 39 / 19694 47.00 0.97 [0.62, 1.52] Subtotal (95% CI) 73 / 32818 83 / 32807 100.00 0.88 [0.64, 1.20]Test for heterogeneity: Chi? = 0.39, df = 1 (P = 0.53)Test for overall effect: Z = 0.80 (P = 0.42)



Göteborg 1982b 21 / 9903 37 / 15708 15.53 0.90 [0.53, 1.54]

Subtotal (95% CI) 155 / 93527 166 / 69652 100.00 0.69 [0.55, 0.86]Test for heterogeneity: Chi? = 1.51, df = 3 (P = 0.68)Test for overall effect: Z = 3.33 (P < 0.001)

0.2 0.5 1 2 5


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 12 Deaths ascribed to breast cancer, 13 years follow-up, younger women (below 50 years of age)



Canada 1980a 82 / 25214 72 / 25216 82.04 1.14 [0.83, 1.56] Subtotal (95% CI) 90 / 28872 88 / 28985 100.00 1.03 [0.77, 1.38]Test for heterogeneity: Chi? = 2.96, df = 1 (P = 0.09)Test for overall effect: Z = 0.18 (P = 0.86)



Göteborg 1982a 18 / 11724 40 / 14217 37.65 0.55 [0.31, 0.95]


0.2 0.5 1 2 5


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 13 Deaths ascribed to breast cancer, 13 years follow-up, elderly women (at least 50 years of age)


01 Medium quality data Malmö 1976 79 / 17430 92 / 17426 46.69 0.86 [0.64, 1.16] Canada 1980b 107 / 19711 105 / 19694 53.31 1.02 [0.78, 1.33]


02 Poor quality data Kopparberg 1977 104 / 29007 88 / 13551 37.76 0.55 [0.42, 0.73] Östergötland 1978 112 / 28229 150 / 26830 48.42 0.71 [0.56, 0.91] Stockholm 1981 42 / 25476 33 / 12840 13.81 0.64 [0.41, 1.01] Subtotal (95% CI) 258 / 82712 271 / 53221 100.00 0.64 [0.54, 0.76]Test for heterogeneity: Chi? = 1.73, df = 2 (P = 0.42)Test for overall effect: Z = 5.10 (P < 0.0001)

0.2 0.5 1 2 5



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 14 Deaths ascribed to any cancer, all women



Canada 1980b 464 / 19711 403 / 19694 28.33 1.15 [1.01, 1.31] Subtotal (95% CI) 1452 / 66013 1425 / 66105 100.00 1.02 [0.95, 1.10]Test for heterogeneity: Chi? = 4.60, df = 2 (P = 0.10)Test for overall effect: Z = 0.57 (P = 0.57)

02 Poor quality data Kopparberg 1977 666 / 39051 319 / 18846 46.00 1.01 [0.88, 1.15] Östergötland 1978 510 / 39034 498 / 37936 54.00 1.00 [0.88, 1.13] Subtotal (95% CI) 1176 / 78085 817 / 56782 100.00 1.00 [0.91, 1.10]Test for heterogeneity: Chi? = 0.02, df = 1 (P = 0.89)Test for overall effect: Z = 0.02 (P = 0.98)

0.5 0.7 1 1.5 2


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 15 Number of mastectomies and tumourectomies



Canada 1980b 448 / 19711 351 / 19694 32.42 1.28 [1.11, 1.46] Subtotal (95% CI) 1424 / 66167 1083 / 66154 100.00 1.31 [1.22, 1.42]Test for heterogeneity: Chi? = 0.28, df = 2 (P = 0.87)Test for overall effect: Z = 6.85 (P < 0.0001)

02 Poor quality data Kopparberg 1977 621 / 39051 216 / 18846 75.41 1.39 [1.19, 1.62] Stockholm 1981 196 / 40318 71 / 19943 24.59 1.37 [1.04, 1.79] Subtotal (95% CI) 817 / 79369 287 / 38789 100.00 1.38 [1.21, 1.58]Test for heterogeneity: Chi? = 0.01, df = 1 (P = 0.92)Test for overall effect: Z = 4.74 (P < 0.0001)

0.5 0.7 1 1.5 2


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 16 Number of mastectomies



Canada 1980b 197 / 19711 176 / 19694 26.20 1.12 [0.91, 1.37] Subtotal (95% CI) 804 / 66167 672 / 66154 100.00 1.20 [1.08, 1.32]Test for heterogeneity: Chi? = 0.86, df = 2 (P = 0.65)Test for overall effect: Z = 3.45 (P < 0.001)

02 Poor quality data Kopparberg 1977 475 / 39051 196 / 18846 76.41 1.17 [0.99, 1.38] Stockholm 1981 143 / 40318 61 / 19943 23.59 1.16 [0.86, 1.56] Subtotal (95% CI) 618 / 79369 257 / 38789 100.00 1.17 [1.01, 1.35]Test for heterogeneity: Chi? = 0.00, df = 1 (P = 0.96)Test for overall effect: Z = 2.09 (P = 0.04)

0.5 0.7 1 1.5 2



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 17 Number treated with radiotherapy


01 Medium quality data Malmö 1976 260 / 21242 209 / 21244 100.00 1.24 [1.04, 1.49] Subtotal (95% CI) 260 / 21242 209 / 21244 100.00 1.24 [1.04, 1.49]Test for heterogeneity: Chi? = 0.00, df = 0 (P = 1.00)Test for overall effect: Z = 2.36 (P = 0.02)

02 Poor quality data Kopparberg 1977 433 / 39051 149 / 18846 100.00 1.40 [1.17, 1.69] Subtotal (95% CI) 433 / 39051 149 / 18846 100.00 1.40 [1.17, 1.69]Test for heterogeneity: Chi? = 0.00, df = 0 (P = 1.00)Test for overall effect: Z = 3.58 (P < 0.001)

0.2 0.5 1 2 5


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 18 Number treated with chemotherapy



02 Poor quality data Kopparberg 1977 226 / 39051 103 / 18846 100.00 1.06 [0.84, 1.34] Subtotal (95% CI) 226 / 39051 103 / 18846 100.00 1.06 [0.84, 1.34]Test for heterogeneity: Chi? = 0.00, df = 0 (P = 1.00)Test for overall effect: Z = 0.48 (P = 0.63)

0.2 0.5 1 2 5


Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 19 Number treated with hormone therapy



02 Poor quality data Kopparberg 1977 8 / 39051 13 / 18846 100.00 0.30 [0.12, 0.72] Subtotal (95% CI) 8 / 39051 13 / 18846 100.00 0.30 [0.12, 0.72]Test for heterogeneity: Chi? = 0.00, df = 0 (P = 1.00)Test for overall effect: Z = 2.70 (P < 0.01)

0.1 0.2 0.5 1 2 5 10



Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 20 Mortality among breast cancer patients, 7 years follow-up

Study Treatment Control RR (fixed) Weight RR (fixed)or sub-category n / N n / N 95% CI % 95% CI

01 Mortality from cancers other than breast cancer Kopparberg 1977 13 / 674 3 / 304 54.63 1.95 [0.56, 6.81]

Östergötland 1978 12 / 621 3 / 464 45.37 2.99 [0.85, 10.53]

Subtotal (95% CI) 25 / 1295 6 / 768 100.00 2.42 [1.00, 5.85]


02 Mortality from causes other than breast cancer Kopparberg 1977 47 / 674 15 / 304 48.73 1.41 [0.80, 2.49]

Östergötland 1978 34 / 621 19 / 464 51.27 1.34 [0.77, 2.31]


0.01 0.1 1 10 100

Favours treatment Favours control

Review: Screening for breast cancer with mammography (Lancet, Sept 2001)Comparison: 01 Screening with mammography versus no screening Outcome: 21 Results for flawed trials


01 Overall mortality, 7 years follow-up New York 1963 890 / 31000 940 / 31000 38.00 0.95 [0.87, 1.04]

Edinburgh 1978 1274 / 23226 1490 / 21904 62.00 0.81 [0.75, 0.87]

02 Overall mortality, 13 years follow-up New York 1963 2062 / 30239 2116 / 30765 100.00 0.99 [0.94, 1.05]

03 Deaths ascribed to breast cancer, 7 years follow-up New York 1963 81 / 31000 124 / 31000 61.32 0.65 [0.49, 0.86]

Edinburgh 1978 68 / 23226 76 / 21904 38.68 0.84 [0.61, 1.17]

04 Deaths ascribed to breast cancer, 13 years follow-up New York 1963 218 / 31000 262 / 31000 57.21 0.83 [0.70, 1.00]

Edinburgh 1978 176 / 28628 187 / 26015 42.79 0.86 [0.70, 1.05]

05 Deaths ascribed to breast cancer, 7 years follow-up, younger women (below 50 years of age) New York 1963 39 / 14849 48 / 14911 78.51 0.82 [0.54, 1.24] Edinburgh 1978 13 / 5913 13 / 5810 21.49 0.98 [0.46, 2.12]

06 Deaths ascribed to breast cancer, 7 years follow-up, elderly women (at least 50 years of age) New York 1963 52 / 16151 80 / 16089 55.11 0.65 [0.46, 0.92]

Edinburgh 1978 55 / 17313 63 / 16094 44.89 0.81 [0.57, 1.16]

07 Deaths ascribed to breast cancer, 13 years follow-up, younger women (below 50 years of age) New York 1963 64 / 13740 82 / 13740 59.44 0.78 [0.56, 1.08]

Edinburgh 1978 47 / 11479 53 / 10267 40.56 0.79 [0.54, 1.17]

08 Deaths ascribed to breast cancer, 13 years follow-up, elderly women (at least 50 years of age) New York 1963 101 / 16505 130 / 16505 48.20 0.78 [0.60, 1.01]

Edinburgh 1978 129 / 17149 134 / 15748 51.80 0.88 [0.69, 1.12]

09 Deaths ascribed to any cancer, all women New York 1963 791 / 30239 823 / 30765 100.00 0.98 [0.89, 1.08]

10 Number of mastectomies and tumourectomies New York 1963 296 / 31092 284 / 31092 100.00 1.04 [0.89, 1.23]

11 Number of mastectomies New York 1963 276 / 31092 250 / 31092 100.00 1.10 [0.93, 1.31]

12 Number treated with radiotherapy New York 1963 107 / 31092 141 / 31092 68.50 0.76 [0.59, 0.98] Edinburgh 1978 75 / 23226 63 / 21904 31.50 1.12 [0.80, 1.57]

0.1 0.2 0.5 1 2 5 10

Favours screening Favours control

systematic review of screening for breast cancer with … · 2016-11-14 · synopsis mammographic...

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