Datos de la variable información

Breast cancer mortality in Norway after the introduction of mammography screening.

Olsen AH, Lynge E, Njor SH, Kumle M, Waaseth M, Braaten T, Lund E. Int J Cancer. 2013 Jan 1;132(1):208-14.

Summary of methods and results

The authors compared incidence-based breast cancer mortality for invited women in the 4 pilot counties (Oslo, Akershus, Rogaland and Hordaland, termed study group) and not yet invited women in the counties included from 2002 and later (Oppland, Hedmark, Vestfold, Møre og Romsdal and Sogn og Fjordane, termed regional control group). First invitation date was measured at the municipality level, while the remaining data were at an individual level.

Two different approaches were used in the comparison of incidence-based mortality, termed the ‘Follow-up model’ and the ‘Evaluation model’, as described by Nyström et al [111]. In the ‘Follow-up model’, the incidence period was from the first invitation in 1996 until the end of 2001 for women aged 50-64 years when screening started (maximum 6 years), and from the first invitation to the end of 2008 for women aged 65-69 years when screening started (maximum 13 years). The follow-up period for death from incident breast cancer was equal to the incidence period in this model.

In the ‘Evaluation model’, the incidence period for all women was restricted to 1996-2001, i.e. only incidence during the screening age range was counted. Follow-up was similar to that in the ‘Follow-up model’.

To account for the underlying temporal decline in breast cancer mortality in the absence of screening, the rate within each region was first compared to the rate in a

preceding period of similar duration as the study period (1990-1996 for women aged 50- 64 years and 1990-2002 for women aged 65-69, termed historical control groups) and this ratio was subsequently compared between the screening and non-screening counties. The rates were compared using Poisson regression and adjusted for (current) age in 5-year groups.

When counting all breast cancer deaths from disease diagnosed after the first invitation date in each municipality and throughout follow-up (the ‘Follow-up model’) the authors found a rate ratio of 0.93 (95% CI 0.77-1.12). When counting only breast cancer deaths from disease diagnosed during the screening age range, 50-69 years, but still including deaths throughout follow-up (the ‘Evaluation model’) the rate ratio was 0.89 (95% CI 0.71-1.12).

Characterization, strengths and limitations

This study used a design developed and implemented in Denmark by Olsen and Lynge, where the effect measure is a double ratio of rates:

(Study / concurrent control) / (historical study / historical control)

The design has well-established parallels in econometrics (the ‘dif-dif’ design [112]). The Danish documentation [111, 113, 114] emphasizes that the design enables the analysis of screening versus non-screening controlled for historical trends, but that this requires the assumption of no interaction between historical development and area.

The study design allows for a detailed account of underlying person-years and a near complete enumeration of breast cancer deaths as well as at least a partial control for underlying time trends in breast cancer mortality.

The present implementation is inconclusive regarding the choice between Nyström’s ‘Follow-up model’ and ‘Evaluation model’. Njor et al [90] discussed the possible lead time bias of the ‘Evaluation model’. The ‘Evaluation model’ produces the strongest effect measured on the relative scale chosen. Nyström’s evaluation model was proposed in a different context from the Norwegian situation: Nyström et al compared long-time follow-up in a randomized trial between screened and non-screened controls, where the latter had a prevalence screen at the end of the first trial period. As explained by Njor et al [90] analyses where the accrual period and the follow-up period (defined in chapter 4.2) do not coincide are prone to lead time bias. With earlier diagnosis due to screening, more women will have a diagnosis of breast cancer at 50-69 years in the study group than in the control groups, and will be at risk of death from breast cancer during follow-up. This will lead to underestimation of the effect of screening. Although the addition of breast cancer cases diagnosed after the age span of screening seems to be neutral in the comparison between screened and controls, this is only correct if the effect measure were on an additive scale – however here the effect was measured on a

multiplicative scale, generating an estimate of lower effect if cases diagnosed late are included.

Since date of first invitation to screening is measured at the municipality level (first day of screening in each municipality) and not individually, some women who were diagnosed with breast cancer before they received their first invitation (i.e. clinically detected tumors) will be classified as detected after invitation to screening. This will lead to underestimation of the effect of screening.

Attention is given to the possibility that any screening effect has been diluted by frequent use of non-program mammography in the control groups. There is disagreement

about the ability of the available Norwegian data to assess the amount of non-program mammography and how much of this can be reasonably considered to act as replacement for screening and extensive use in the control groups could reduce the estimated

effectiveness by the organized program. However, in studies of incidence-based mortality a shift of cancer detection towards years before the incidence period will deplete the population during the incidence period of some breast cancers and thus remove breast cancer deaths in such cases from the population.

Due to the short period between start of screening in the pilot counties and in the last counties, the contrast in exposure (screening invitation) between the groups will be no more than one to three screening rounds. In combination with a short follow-up for most of the participants, this may have led to underestimation of the effect of the screening program. Since the study was restricted to the first and last counties where screening was implemented, statistical power was limited.

As mentioned above, the model is valid under the assumption of no interaction between period and region, i.e. that the relative decline in mortality over the period should be similar in both regions in the absence of screening. The pilot counties had higher breast cancer incidence rates [104] and lower breast cancer mortality than the rest of the country before screening was implemented. In addition, breast diagnostic centers and multidisciplinary teams were established before screening could start in each county, and would be functional from different time points in the pilot counties and the remaining counties. This may imply that some of the observed risk reduction may be attributed to multidisciplinary teams since any mortality benefit from specialized centers will be greater in the pilot counties, where such centers were present during the whole follow-up. There could also be trend differences in mortality at the county level due to differences in risk factors. A risk factor that differed between counties during the study period was hormone therapy use, which was more prevalent in the pilot counties than the control counties [34]. Since a prescription of hormone therapy has been followed by a

recommendation of mammography examinations, it might also have increased the use of mammography outside the program.

Conclusions

The effect of screening is estimated as an overall non-significant rate ratio of between 0.89 and 0.93, these estimates being based on two different concepts for interpreting the data, and there is uncertainty which model would be preferable. The double ratio design has allowed correction for historical trends, but necessitates an assumption of no

interaction between county and time trend. There are systematic differences in socio- demographic composition and development of health services between screening and control counties, which may distort the comparison in directions that are hard to predict. A widespread non-program mammography use and lack of individual data on invitation date may dilute any screening effect. Duration of both the exposure period and the follow-up period may be too short to provide information on the long-term effectiveness of a fully implemented screening program. Finally, it is hard to distinguish any effect of screening from effects of the concomitant organization of multidisciplinary specialized teams.

Mammography activity in Norway 1983 to 2008.

Lynge E, Braaten T, Njor SH, Olsen AH, Kumle M, Waaseth M, Lund E. Acta Oncol. 2011 Oct;50(7):1062-7.

Summary of methods and results

This is a report of total mammographic activities. The aim of the study was to investigate the extent of all mammographic activity in Norway during the period 1983-2008, and to estimate the impact of that activity on the effectiveness of NBCSP. The authors used publicly available numbers and data from NOWAC to estimate the number of women who had opportunistic screening prior to NBCSP implementation. Public sources included reports from the Norwegian Radiation Protection Agency (NRPA), summary data from the NBCSP, a report from the Cancer Registry of Norway and a report from the University College in Oslo. The NOWAC sample included women who responded to a questionnaire with questions about mammography use in 1996, 1997-1998, and 2002. It is stated that of 121 683 invited women in screening relevant ages (this is not specified, but data are presented for ages 40-69), 70% responded to the mammography questions. However, data are presented for 94 211 women, which is 77% of 121 683. In 1996 and 1997/1998 women were asked about regular use of mammography, and could answer no, yes – every second year or more often, and yes – with an interval of more than two years. In 2002, the question was about ever/never use of mammography.

The total number of mammography examinations in Norway registered by the NRPA was 10 000 in 1983, 80 000 in 1988, 221 210 in 1993, and 349 057 in 2002. For 1983-1993, the number of women examined was estimated by dividing the number of examinations by two, giving 5000 women examined in 1983, 40 000 in 1988, and 110 605 in 1993. For 2002, an algorithm developed by Hofvind was used to estimate that 131 758 women were examined outside NBCSP. The annual number of examined women in 1996 was also estimated from the NOWAC data, and compared to the numbers from NRPA. In 1996, 25% of 11 819 NOWAC participants 40-69 years had regular mammography with no more than 2 years interval, and 18% had regular mammography with more than two years interval. With the assumption that more than two years interval can be regarded as every fourth year, the authors estimate that 119 000 women aged 40- 69 years were examined in Norway in 1996. The authors conclude that this number is comparable to the 110 605 women examined according to NRPA in 1993, and that the different sources of data collectively indicate that at least 40% of Norwegian women had regular mammography prior to their first NBCSP invitation.

Only the NOWAC data could be used to examine mammography use separately for the pilot counties and the non-pilot counties. In 1996, 47% of NOWAC participants aged 50-69 used mammography regularly in the pilot counties, compared to 40% in the non-pilot counties. In 1997-98, the numbers were 73% and 47%, respectively. In 2002, 97.5% of NOWAC participants 50-69 years in the pilot counties reported ever use of mammography, compared to 87.4% of women in the remaining NBCSP counties (combined 92%), and 79.3% in the counties where screening had not yet been implemented. In the NBCSP, 64% of attending women reported ever use of mammography before their first NBCSP attendance.

The authors used these numbers to estimate that a true risk reduction by screening of 25%, would be observed in a dif-dif design with three unexposed groups as only 11% reduction with their estimated level of opportunistic screening before and in parallel with the NBCSP implementation. The assumptions in those calculations were: Breast cancer mortality rate of 71/100 000 person-years before screening and 68/100 000 person-years

during the screening period if screening had not been implemented; similar effects of program and opportunistic screening; 40% opportunistic screening in 1996 across the country; 92% screened in the NBCSP counties and 64% screened in the non-NBCSP counties after 1996.

Characterization, strengths and limitations

This is a primarily descriptive study with comparison of information on mammography use from several sources.

The study provides an overview on the available information on opportunistic screening in Norway. The data from NOWAC have not been presented elsewhere and adds new information to a field with scarce information.

The comparison of regular non-program mammography in the pilot counties and other counties in different years are based on small numbers from the NOWAC. The questions on mammography use in 1996 and 1997-98 had no clear response alternative for women who had used mammography, but not at a regular basis. Furthermore, the question in the 2002 questionnaire did not measure regular mammography use, and the answers to this question should not be directly compared to those from 1996 and 1997-98. No information is provided concerning the algorithm used to estimate the number of women examined in 2002 from the NRPA data.

The comparison between the estimated 119 000 number of women 50-69 years examined with mammography in 1996 and the 110 605 women examined in 1993 according to NRPA, does not take into account that the number provided by NRPA includes all age groups and also clinical mammography. This implies that the estimate from NOWAC data may be quite a lot higher than the NRPA data from 1993. On the other hand, some NOWAC participants in 1996 had probably attended the NBCSP before responding to the questionnaire.

In the calculations of the expected effect of NBCSP in the presence of extensive opportunistic screening, the reported proportion of women with ever use of mammography were used as a measure of the proportion screened (through NBCSP or opportunistic screening). It is not known how many of the 64% NBCSP attendants reporting ever use of mammography prior to NBCSP should be classified as opportunistically screened, since only the time since previous mammography has been reported [76]. In addition, non-program screening could influence incidence-based breast cancer mortality in opposite directions through different mechanisms, as discussed in the evaluation of the study by Olsen et al above.

Conclusions

The study documents widespread use of mammography screening outside the NBCSP, but how much of this should be considered as non-program screening and the expected effectiveness of such screening remains unclear. The use of mammography in any choice of control group from the appropriate age groups in Norway would be higher than has been the mammography use in the control groups in the historic randomized trials.

Modern mammography screening and breast cancer mortality: population study.

Weedon-Fekjær H, Romundstad PR, Vatten LJ. BMJ. 2014 Jun 17;348:g3701.

Summary of methods and results

The authors compared breast cancer mortality among invited and not invited women in an open cohort consisting of all Norwegian women followed while they were aged 50-79 years during 1986-2009. Invitation date for screening, date of breast cancer diagnosis and date of death from breast cancer were measured at an individual level. Person-time was measured at an ecologic level for each combination of calendar year, birth cohort and county.

Poisson regression with adjustment for age, birth year, calendar year at death, and county was used to estimate the mortality from breast cancer for invited women and non- invited women. To estimate the breast cancer mortality from 1996 to 2009 attributable to breast cancers diagnosed after invitation (incidence-based mortality), the authors used a model offset to adjust for the expected proportion of deaths caused by breast cancer diagnosed during the time period since first invitation. To avoid bias from lead time, this expected proportion was estimated from the distribution of time from diagnosis to death from breast cancer among women diagnosed before screening invitation, assuming that the time from diagnosis to death from breast cancer would be equal in the absence of screening. The model offset was estimated separately for women 50-59, 60-69 and 70-79 years at death and based on pre-invitation diagnoses from two different periods; 1990- 1994 and 1996-2009, with very similar results.

Calculations based on simulated data confirmed the validity of the approach. Several sensitivity analyses were conducted to assess the impact of different assumptions, such as different ways of including covariates, varying the effect of screening invitation by calendar year, time since first invitation and time since last invitation, as well as expansion of the study age group to 40-85 years. Numbers needed to invite for screening to prevent one death from breast cancer was calculated according to the Stanford CISNET model [115, 116] using the national breast cancer mortality in 2009 and the estimated relative mortality reduction as the basis for the calculation.

Breast cancer mortality after invitation to screening was 28% lower than for women who were not invited (MRR 0.72, 95% CI 0.64 to 0.79). A lower mortality was observed also after screening invitations had ended, although less pronounced (for women 75-79 years MRR was 0.79, 95% CI 0.57 to 1.01). Inclusion of covariates did not change the estimates substantially. Most sensitivity analyses gave the same result as the primary analysis. Numbers needed to invite to prevent one death from breast cancer among women 50-89 years was estimated to 368 (95% CI 266 to 508).

Characterization, strengths and limitations

This study is based on an original epidemiological-statistical approach developed by the authors and documented in web appendices to this BMJ article. The approach – a Poisson regression model with non-screening breast cancer mortality as a shared underlying latent variable – allows inclusion of the individual experience of all women in the relevant age groups over a period (1986-2009), thus including a significant period before screening started.

The developed method may be considered as an original modern version of the classical technique of indirect standardization based on comparing mortality in a study group to that expected if the mortality was as in the standard (here: non-screening) group.

The development is supplemented with tests on simulated data (confirming that the postulated effects may be recovered by this approach) as well as careful and wide-ranging sensitivity analyses to assess the various model choices, documenting considerable robustness of the approach. The authors developed a detailed protocol before they had access to the data and deposited this protocol with the Norwegian Research Council to ensure that the modeling was not unduly influenced by fishing expeditions in the data. The study was conducted according to the study protocol.

Misclassification of invitation date should be minimal, since this was measured at an individual level. The extent of exposure misclassification due to non-program mammography is unknown, and the potential impact on the results is difficult to assess. As discussed in the evaluation of the study by Olsen et al, non-program screening in women not yet invited may influence the estimated association in different ways: Preventing some deaths from breast cancer in women whose cancer would have been clinically detected before their first invitation may lead to underestimation of the program’s effectiveness. Earlier detection by opportunistic screening will move some breast cancer diagnoses to the non-invited group that would not be clinically detected until after the first invitation, which may lead to overestimation of the effectiveness. Non-