Statistical analysis plan for the follow-up phase

2.1 Background, and rationale for long-term follow-up

In the UK, women of age 50-70 are invited about every 3 years for two-view digital mammographic screening, with the first invitation generally at ages 50-52 and the 7th and last at ages 68-70. The Independent UK panel on breast cancer screening concluded in 2012 that 7 such invitations at ages 50-70 would reduce breast cancer mortality by about 43 per 10,000 (an average of 6 per 10,000 per invitation), but that the effects of additional screening outside the range 50-70 remained uncertain.¹

AgeX seeks to address this uncertainty by providing large-scale randomised evidence on the effects of one additional screening at ages 47-49 and, separately, the effects of one additional screening at 71-73.  It randomised 4.5 million women (2.8 million younger and 1.7 million older), half allocated to be sent one additional screening invitation and half not.

Of them, 3 million (2 million younger and 1 million older) are included in the main analyses population (Section 5). Randomisation excludes all possibility of bias between invitees and controls, and appropriate analyses (Section 6) can yield unbiased estimates of the effects of one additional screening visit, and of one additional screening invitation.

Randomisation lasted from mid-2009 (when the pilot phase began) to March 2020, when COVID temporarily disrupted the national breast screening program. Screening the last few invitees was delayed by this disruption for some months but was eventually completed. By 2024 the entire AgeX database had been consolidated and linked for long-term (purely electronic) follow-up to all relevant national datasets, and pre-randomisation characteristics had been defined from sources that cannot have been affected by the random allocation.

To assess the long-term (for a decade or two after randomisation) direct and indirect effects of one additional screening, AgeX is continuing low-cost electronic follow-up (involving no contact with participants). This involves linkage to routinely collected NHS England records of breast cancer incidence and treatment, of hospital episode statistics, and of cause-specific mortality (as coded by the Office for National Statistics), but no other contact with the NHS or the screening program. 

The AgeX data monitoring and ethics committee (DMEC) will continue during long-term electronic follow-up to review annually (as it has been doing throughout the entire study) confidential interim analyses, particularly of mortality. The first two published reports on mortality are scheduled to be in 2027-28 (the interim analysis, of mortality to 12.2026) and 2032-33 (the final analysis, of mortality to 12.2031) unless the DMEC recommends release of earlier mortality results.

Because recruitment was completed some years before scientifically informative evidence on mortality could reasonably have been expected, in reports of the scheduled interim and final mortality analyses no statistical allowance will be made for the DMEC having periodically examined the data. For, follow-up will continue anyway, so the interim and final analyses cannot be affected by any DMEC reports. This 2024 statistical analysis plan (SAP) is for the 2025-33 follow-up phase of AgeX. It describes the pre-specified primary and main subsidiary analyses, based on version 7.0 of the AgeX study protocol (earlier versions specified similar analyses), and adheres to guidelines for SAP content.²

2.2 Primary objective

The primary objective is to assess long-term effects (for a decade or two, depending on each woman’s date of randomisation) of one additional screening on breast cancer mortality. The primary analyses will assess the effects of actually having had one additional screening visit, and parallel analyses will assess the effects of having being randomly allocated to receive one additional screening invitation.

2.3 Main subsidiary objectives

The main subsidiary objectives are to assess long-term effects of one additional screening visit on breast cancer incidence (partly to help assess the extent of over-diagnosis) and on the use of mastectomy, of breast-related radiotherapy, and of systemic breast cancer therapy, particularly chemotherapy (to assess the net effects of screening on the eventual extent to which these treatments are given).

Again, analyses parallel to these main subsidiary analyses will assess the effect of one additional screening invitation. Health economic analyses will accompany the final analyses of breast cancer incidence, treatment and mortality.

3.1 Trial design

AgeX comprises two large cluster-randomised trials (one in older and one in younger women), each with about 20,000 small clusters of women. Within each trial, each cluster was randomly allocated (as if on the toss of a coin) to receive, or not, one additional invitation to mammographic screening.  

3.2 Randomisation

The breast screening programme (BSP) in England is delivered by around 80 breast screening units (BSUs); the exact number fluctuates. They could not join AgeX until they were using digital mammography. AgeX began in 2009 with a pilot study of the acceptability of cluster randomisation in 5 BSUs. By 2013 it had been extended to around 60 BSUs (after which the number of participating BSUs remained approximately stable; all were in England), and it randomised about 0.5 million women annually from then until March 2020.

3.2.1 Definition of age as a whole number

Within the BSP, a national database is used to create screening invitation batches every few weeks for each BSU. For each of the BSUs recruiting into AgeX, typical invitation batches included a few hundred names spanning ages 47-73 (which the BSP defined in whole years by year of birth until mid-study, and by exact date of birth thereafter: Annex 3 to study protocol). Some batches also included small numbers of women aged 45-46, classified in this SAP as 47, or aged 74-75, classified in this SAP as 73.

3.2.2 Definition of clusters for randomisation

The intent was that those aged 50-70 would not be newly entering AgeX and would instead all be sent routine screening invitations (regardless of whether they were already in AgeX), but that the two “clusters” of younger or older women would both enter the study, with either the younger cluster or the older cluster invited for screening. The program that generated the batch defined which women were newly entering AgeX, and decided randomly, in a 50:50 ratio, which of the two clusters would be invitees and which would be controls. (The older and the younger cluster do not get compared.)

3.3 Analysis as two separate trials

The findings from AgeX will be monitored, analysed and reported as two entirely separate trials. One is a trial among younger women (randomised at age 47-49 to be invitees or controls) of the effect of one additional screening about 3 years before routine screening would normally have begun. The other is a trial among older women (randomised at age 71-73 to be invitees or controls) of the effects of one additional screening about 3 years after routine screening would normally have ended. Thus, the younger clusters in AgeX get compared only with each other, and never with any of the older clusters; likewise, the older clusters get compared only with each other.

3.4 Sample size

AgeX did not have a pre-determined sample size. Instead, by design, randomisation could have continued for as long as substantial uncertainty about the results persisted, unless the data monitoring and ethics committee advised otherwise.

From 2009-20, around 20,000 clusters containing 2.8 million younger women were randomly allocated to be invited or not for one additional screening. Likewise, around 20,000 clusters containing 1.7 million older women were randomly allocated to be invited or not for one additional screening.

The main analyses population will include only the 2 million younger women and 1 million older women who had been eligible and linkable to NHS England datasets, with no record there of prior cancer or breast disease, and who were considered likely to attend screening if invited (based on uptake of their previous breast or cervical screening invitation). These criteria depended entirely on information that could not have been affected by the random allocation. Details of those included and excluded are in Section 5.2. Those excluded will be analysed in appropriate ways (Section 6.8), but not as part of the main analyses.

3.5 Hypothesis framework

For each of the main analyses, the null hypothesis will be no effect of one additional screening.

3.6 Need for long-term follow-up of mortality

Long-term follow-up is necessary to assess the eventual effects of one additional screening on breast cancer incidence, breast cancer treatment, and, particularly, breast cancer mortality. As little effect on breast cancer mortality should be expected until years 5-9 and 10-14 after randomisation, prolonged follow-up of mortality will be required, first to 12.2026 and then to 12.2031. 

3.7 Interim analyses and “alpha-spending”

Analyses of breast cancer incidence and treatment will be reported in 2025-26, before any unblinded analyses of mortality are reported, but electronic follow-up of breast cancer incidence and treatment will continue after that date.

Unless the DMEC recommends release of earlier mortality results, the only interim report on mortality will be that scheduled to be released in 2027-28, based on analyses of mortality to 12.2026, and the second and final report on mortality will be that scheduled to be released in 2032-33, based on analyses of mortality to 12.2031. The final report on mortality will be accompanied by updated analyses of breast cancer incidence and treatment, and by health economic analyses.

P-value calculations and confidence intervals in the final analyses will make no formal “alpha-spending” statistical allowance for the existence of previous analyses, as electronic follow-up will continue regardless of any interim findings.

4.1 Adjustment of P-values for multiplicity, and confidence intervals

In presentation of results (with the exception of the safety analyses of hundreds of different causes of death; Section 6.9), formal allowance will not be made for multiple testing.  However, allowance may, where appropriate, be made for multiple testing and any other potential sources of bias in discussion and interpretation of results. Other things being equal, the more extreme the P-value the more reliable the evidence will be considered to be of a real effect on breast-cancer-related outcomes. Although all confidence intervals will be 95%, this does not imply that P-values slightly above or slightly below 0.05 will be interpreted very differently.

4.2 Main analyses population

All analyses will strictly respect the random allocation, thereby avoiding bias. The main analyses are those of the primary and main subsidiary endpoints (Sections 6.1 and 6.2). These will be restricted to the “main analyses population” (Section 5.2), which includes only the 2 million younger and 1 million older participants who had been eligible and linkable to NHS England datasets, with no record there of prior cancer or breast disease, and who were considered likely to attend screening if invited (based on uptake of their previous breast or cervical screening invitation). Details of those included and excluded are in Table 1. All these inclusions and exclusions were based on information that could not have been affected by the random allocation.

4.3 Adherence and protocol deviations

Invitees and non-invitees (controls) are defined as those who were randomly allocated to be, or not to be, invited, regardless of whether an invitation actually reached them. Within the main analyses population, let P and p denote, respectively, the proportions of the invitees and controls who (without having had a diagnosis of breast cancer recorded as being after randomisation but before getting screened) actually had an NHS breast screening clinic visit within one year of randomisation. The proportion of invitees adherent to their random allocation is then P, the proportion of controls adherent to their random allocation is 1-p, and the difference P-p indicates the effectiveness of the random allocation as a determinant of screening rates.

The proportions of invitees and of controls screened by various times after randomisation will be described by Kaplan-Meier plots of proportions having had a screening visit against time since randomisation (calculated from routinely collected NHS England electronic records of screening visits). The delay between randomisation and screening for those who would attend within 1 year if and only if invited will also be estimated (see Section 6.3.1 on adherence-corrected analyses).

5.1 Eligibility for cluster randomisation

Women were eligible for cluster randomisation if they were aged 47-49 or 71-73 (see Section 3.2.1 for the definition of age) and registered with an NHS general practitioner (a necessity for routine NHS breast screening invitations).

5.2 Patient throughput from randomisation to inclusion in the main analyses population

The flow of invitees and controls from randomisation to inclusion in the main analyses population is shown in Table 1, which gives more details than a standard CONSORT flow-chart. Briefly,  women were included if, when randomised, they were the right age, alive, linkable to routinely collected NHS England electronic records, without a history of cancer or other breast disease, and (based on their previous screening history) likely to accept if invited. For, inclusion of women who would be unlikely to accept if invited would dilute any effects of screening, reducing the sensitivity of analyses that compare all invitees vs all controls. The requirement of being likely to accept if invited excluded older women who had missed their previous breast screening invitation (or whose last invitation was not 1.0-5.0 years ago). It also excluded younger women who had no NHS record of cervical screening in the past 5 years (despite having no NHS record of having had a hysterectomy).

All these exclusion criteria were based unbiasedly on information recorded before randomisation, all were defined blind to analyses of mortality differences between invitees and controls, and no exclusion criterion was significantly unbalanced between invitees and controls (Table 1).

5.3 Follow-up, and loss to follow-up

Information on ICD-coded mortality and cancer registration, and on which participants still being followed up, is sent to AgeX regularly every 3 months by NHS England. The average lag in this is assumed in AgeX analyses to be 3 months for death and 15 months for cancer diagnosis. Other linked datasets (Section 6.2) generally arrive about annually.

If a woman chooses to opt out of having her further NHS records used for research then she will cease to be mentioned in all subsequent datasets sent to AgeX (and even her opt-out will not be mentioned), so the AgeX mortality and cancer onset analyses stop 3 and 15 months before she was last included.

If a woman is recorded by NHS England as having moved permanently or semi-permanently from England to another part of the UK (or abroad) then this too is reported, and the AgeX analyses stop at her emigration date unless death, cancer or return is reported.

Analyses of mortality and cancer incidence will include all cases reported to AgeX, regardless of whether follow-up was thought to have stopped. Any slight uncertainty about effective numbers at risk does not bias the comparison of invitees versus controls. Estimated proportions lost to follow-up for reasons other than mortality will be plotted against year since randomisation.

5.4 Baseline characteristics

The only baseline characteristics planned to be used are those that defined the exclusion criteria used in Table 1. Further subdivision of the younger and the older women by age would not be usefully informative, as the age ranges 47-49 and 71-73 are extremely narrow.

6.1 Definition of the primary endpoint

The primary endpoint is breast cancer mortality, based on deaths coded by the Office of National Statistics (ONS) as having breast cancer (ICD-10 C50 or ICD-11 2C6) as the underlying cause. Thus, a death will be considered to have been from breast cancer if and only if breast cancer had been coded as the underlying cause in the final ONS death registration records. The primary analyses focus on breast cancer deaths in particular time periods (Section 6.3.3).

6.2 Definition of the main subsidiary endpoints

The main subsidiary endpoints are:

• invasive breast cancer ( ICD-10 C50 or ICD-11 2C6), from NHS England cancer registration records (overall, and subdivided by tumour characteristics such as diameter, grade, ER status and stage);
• in situ breast cancer (ICD-10 D05 or ICD-11 2E65), which may result in surgery or radiotherapy, again from these cancer registration records;
• use of mastectomy (OPCS-4 B27) that was recorded in the NHS England hospital episode statistics (HES);
• use of systemic breast cancer therapy, particularly breast cancer chemotherapy (OPCS-4 X70-3, X352, X373, X384, Z511-2), that was recorded in these hospital episode statistics or recorded in the NHS England systemic anti-cancer therapy (SACT) dataset; and
• use of radiotherapy for breast disease (ICD10 C50, D05, D24, N60-64 or ICD11 2C6, 2E65, 2F30, GB20-23) that was recorded in the NHS England radiotherapy data set (RTDS).

If NHS general practice records become conveniently linkable then any relevant information from them could eventually also be incorporated into the AgeX analyses of breast cancer treatments given, but treatment outside the NHS may well never be captured.

6.3 Methods for the primary analyses

After the exclusions described in Sections 4.2 and 5.2, the primary and main subsidiary analyses will be of the effects of actually having one additional screening visit. Parallel analyses will be provided of the effects of being randomly allocated to receive one additional screening invitation (Section 6.3.2).

6.3.1 Adherence-corrected analyses of the effects of one additional screening VISIT

Estimates of the effect of one additional screening visit on breast cancer mortality will use the method of Cuzick et al³ to allow for non-adherence, which avoids assuming similarity between those adherent and non-adherent to the random allocation. The aim of adherence-corrected analyses is to estimate the actual effects of a screening visit among those women who would have had a screening visit if, and only if, randomly allocated to be invited for screening. (Screening does not include mammography after a breast cancer has been diagnosed.)

Some women, who may well be atypical in unknown but relevant ways, would not get screened, regardless of what their random allocation happened to be. Some other women, perhaps atypical in other relevant ways, would get screened anyway, again regardless of what their random allocation would be. All others would have a screening visit if, and only if, randomly allocated to be invited. *

Adherence-corrected analyses of the effects of actually having, vs not having, a screening visit involve comparing (A – B) vs (D – C), with groups A, B, C and D as defined in the table. For, subtraction of group B is equivalent to removing from group A those who would have been screened even if not invited, leaving those who would have a screening visit if, and only if, invited. Likewise, subtraction of C is equivalent to removing from D those who would not have been screened even if allocated to be invited, again leaving those who would have a screening visit if, and only if, allocated to be invited. *

This comparison of (A – B) vs (D – C) assesses unbiasedly the full effects among those who would have a screening visit if, and only if, allocated to be invited, without assuming that groups A, B, C and D are comparable with each other.³ This method of adjustment for adherence has little or no effect on the statistical power to detect any differences in breast cancer mortality between invitees and controls.

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* There might also, at least in theory, be a tiny group who, perversely, would all get exactly the opposite of whatever their random allocation happened to be. Ideally these non-adherent women would be excluded when analysing the results, but as they are not individually identifiable they cannot be. This does not, however, introduce any bias at all into the adherence-corrected estimates of the proportional effect of screening (as the adherence correction subtracts this tiny non-adherent group from both sides of the comparison).

6.3.2 Intent-to-treat analyses of the effects of one additional screening INVITATION

Parallel analyses will be provided of the effects of being randomly allocated to receive one additional screening invitation. These parallel analyses are modified intent-to-treat (mITT) analyses; “modified” indicates restriction to the 3 million included invitees and controls, rather than all 4.5 million women originally randomised.

6.3.3 Focus on appropriate time periods

To assess the eventual effects of one additional screening visit (or of one additional screening invitation) on breast cancer mortality, follow-up must be long (a decade or two by the time of the final analyses, depending on the year of recruitment) and the analyses of breast cancer mortality must be strictly unbiased and as sensitive as possible, focusing on the periods in which an appreciable effect can reasonably be expected.

No material effect of the random allocation should be expected on breast cancer mortality during the first few years after randomisation. Hence, the primary analyses are restricted to the later breast cancer deaths (Sections 6.3.4 to 6.3.5).

A few years after just one single additional screening invitation, the annual incidence rates of newly diagnosed breast cancer may well become similar in invitees and in controls. No material effect of the random allocation should be expected on mortality from breast cancers that are diagnosed after this convergence of incidence rates. Hence, the primary analyses are further restricted to deaths from breast cancers that had been diagnosed only a few years after randomisation (Sections 6.3.4 to 6.3.5).

6.3.4 Tabulation of breast cancer deaths in younger women

In the younger women (randomised at ages 47-49) the annual incidence rates of new breast cancer became similar by year 4 after randomisation, because by then all the invitees and all the controls should have been invited recently for routine screening (at ages about 50-52). This routine screening invitation makes the cumulative incidence in controls catch up with that in invitees within 4 years of randomisation.

The numbers of breast cancer deaths among younger women will therefore be tabulated, with and without adherence correction, both by years from randomisation until diagnosis of the fatal cancer and by age at death, in the format of Table 2. The adherence-corrected tabulation addresses the effect of actually having one additional screening visit, and the parallel (mITT) tabulation, without adherence correction, addresses the effect of having been allocated one additional screening invitation. Analyses of both of these tabulations will focus on mortality after reaching age 55 from a breast cancer known to have been diagnosed < 4 years after randomisation, with the primary analysis being that of the adherence-corrected table. Dates of diagnosis will be taken from the linked national datasets (primarily using cancer registry data, but using other datasets as registry data if these provide a date of diagnosis and the registries do not).

In Table 2, hypothetical numbers of breast cancer deaths (not adherence-corrected) are inserted into the subtotals for mortality from breast cancers diagnosed during the first 4 years after randomisation and those diagnosed later (or at an unknown time). These illustrate what the final results after follow-up to 12.2031 might be if random allocation to one additional screening invitation at ages 47-49 reduced by about 20% the probability of having a breast cancer diagnosed < 4 years after randomisation that caused death after reaching age 55 (shaded parts of Table 2) but had no effect on the other breast cancer deaths.

Regardless of whether such a 20% difference is considered plausible, any effect of one additional screening invitation on breast cancer mortality may well chiefly affect just the results in the shaded parts of Table 2. The same would be true of the adherence-corrected version of Table 2. Hence, the primary analysis will focus just on the sum of the adherence-corrected results in the shaded parts.

Three-yearly mammographic screening detects a higher proportion of all ER+ breast cancers than of all ER– breast cancers. Hence, subdivision of the breast cancer deaths by ER status (ER+, ER– or unknown) will also be tabulated in the same format as for all breast cancer deaths, but chief emphasis will be on the overall breast cancer mortality results, regardless of ER status.

6.3.5 Tabulation of breast cancer deaths in older women

In the older women (randomised at age 71-73), no further invitations were scheduled for the controls. Hence, the time when the annual incidence should be expected to become similar in invitees and controls cannot be predicted as easily as in the younger women. Nevertheless, lacking further information, the analyses of breast cancer mortality in the older women will involve the same methods and format as those in the younger women, except that the age groups will be 70-74 (when little effect on breast cancer mortality should be expected), 75-79, 80-84 and 85+.

6.3.6 Kaplan-Meier plots

For both younger and older women, adherence-corrected Kaplan-Meier plots of cumulative event rates by time since randomisation will be given for death from a breast cancer diagnosed < 4 years after randomisation, and for death from a breast cancer diagnosed later (or at an unknown time). These describe the effects of one additional screening visit. Parallel results will also be given for mITT analyses of the effects of one additional screening invitation (without correction for adherence).

6.3.7 Summary of the definitions of the primary analyses

The interim and final primary analyses will include only the 2 million younger and 1 million older participants who had been eligible and linkable to NHS England datasets, with no record there of prior cancer or breast disease, and who were considered by pre-defined criteria likely to attend screening if invited (Section 5.2; Table 1).

These will be adherence-corrected analyses of the effect of one additional screening visit (Section 6.3.1). Parallel “mITT” analyses will also be given of the effect of being allocated one additional screening invitation.

The primary analyses will be restricted to deaths from a breast cancer diagnosed < 4 years after randomisation that occurred after reaching age 55 for younger women (Section 6.3.4; Table 2) and after reaching age 75 for older women (Section 6.3.5).

6.4 Methods for the main subsidiary analyses

For both younger and older women, adherence-corrected Kaplan-Meier plots of cumulative (first) event rates by time since randomisation will provide the main subsidiary analyses of the effects of one additional screening visit on breast cancer incidence and on the eventual use of mastectomy, of radiotherapy, and of systemic therapy (particularly chemotherapy). Again, parallel results will also be given for mITT analyses of the effects of one additional screening invitation (without correction for adherence).  The final primary and subsidiary analyses will be accompanied by appropriate health economic analyses.

6.5 Missing data

As record linkage is reliable and the endpoints are defined to be of the recorded numbers of events in the linked national datasets there can be no missing data for the primary and main subsidiary endpoints, except for those women no longer available for record linkage (see Section 5.3).

6.6 Allowance for clustering in analyses of breast cancer mortality

Wherever numbers of deaths from breast cancer in invitees and in controls are to be compared, calculation of the statistical significance of the comparison will make appropriate allowance for the cluster randomisation. This will make little difference to calculations of statistical significance or of confidence intervals, as the average numbers of breast cancer deaths per cluster will be small even in the final analyses.

For the hypothetical final numbers in Table 2 for younger women the average number of breast cancer deaths per cluster in the primary analyses would be only 0.1, and for the older women it may well be comparably small. Hence, although AgeX is cluster-randomised the comparisons of breast cancer mortality will have virtually the same statistical power as individually randomised comparisons of similar size would have had.

As, however, the numbers excluded for certain particular reasons were substantial, the analyses of these numbers of exclusions (Table 1) had to make appropriate allowance for clustering.

6.7 Additional analyses of all-cause mortality

For both younger and older women analyses of all-cause mortality will be reported. However, they are unlikely to be usefully informative and will not be considered relevant to the interpretation of the primary analyses of breast cancer mortality. For, in both younger and older women, more than 90% of deaths are expected to be from causes other than breast cancer (based on the blinded mortality data to 2024), so there will be negligibly small power for AgeX to assess directly the effect of additional breast screening on all-cause mortality.

6.8 Additional analyses: women not in the main analyses population

Of the 4.5 million women randomised, 3.0 million are in the main analyses population and 1.5 million are not. Analyses of adherence and of outcomes in various categories of those excluded could be of interest and will be reported, but will not be part of the primary and main subsidiary analyses and will not contribute directly to the interpretation of these analyses.

6.9 Safety analyses

Given the statistical difficulty of assessing the effects of screening on mortality from breast cancer, there can be no realistic expectation of demonstrating directly any effects of breast screening on mortality from any other causes, or on all-cause mortality. Nevertheless, safety analyses will be reported that, both in younger and, separately, in older women, report the numbers of deaths from each 3-character ICD category with at least 10 deaths, and of mortality from the aggregate of all causes other than breast cancer. Any P-values ≤ 0.05 generated by these hundreds of analyses will, however, be accompanied by Bonferroni corrections to help allow for the multiplicity of such comparisons.

6.10 Statistical software

SAS version ≥ 9.4, StataNow version ≥1 8.5 and R Studio version ≥ 4.2.3 will be used.

7.1 Plausible reductions in breast cancer mortality

In 2012, the UK panel on breast cancer screening estimated an absolute reduction in breast cancer mortality of 0.6 per 1000 women per routine 3-yearly invitation in the age range 50-70 (total 4.3 per 1000 for 7 such invitations).¹ The probability that mammography will detect a cancer is, however, only about one-third as great at ages 47-49 as at ages 71-73. This, together with the panel’s estimate, would suggest absolute reductions of about 0.3 per 1000 younger invitees and 0.9 per 1000 older invitees.

UK mortality from breast cancer in middle age may well, however, be about one-third lower in the 2020s than it was in the 2000s. So, reductions in mortality of only about 0.2 per 1000 younger invitees and 0.6 per 1000 older invitees can plausibly be expected during follow-up in AgeX.

The plausible reductions outlined above provide the basis for the AgeX power calculations, and adjustments for adherence (Section 6.3.1) have little or no effect on this power (as they do not, in expectation, alter the absolute difference between the two treatment groups in numbers of relevant breast cancer deaths, or in the variance of this difference).

However, as entry into AgeX has already ended and the main analyses population has already been defined (Table 1), the statistical power depends entirely on how big the effect on breast cancer mortality of just one additional screening visit will actually be, which will not be known until after the final results emerge.

7.2 Power calculations for the final primary analyses of breast cancer mortality

The statistical power of the final primary analysis, with follow-up of mortality to 12.2031, will be greater than the statistical power of the interim primary analysis with follow-up only to 12.2026, unless there is little additional benefit after 2026. The expectation of an absolute reduction of 0.2 per 1000 younger invitees is consistent with the hypothetical numbers in Table 2, which underlie this SAP.

In Table 2, the absolute reduction of 0.2 breast cancer deaths per 1000 invitees is driven by the 20% reduction after age 55 from a cancer diagnosed < 4 years after randomisation, involving 400 vs 500 deaths expected before age 60 and 400 vs 500 deaths after age 60. If a total of 800 vs 1000 deaths is expected, this gives a 98% chance of achieving P < 0.01 and a 92% chance of achieving P <0.001.

The power for the final analysis, with follow-up to 12.2031, to detect an absolute reduction of 0.6 breast cancer deaths per 1000 older invitees would be at least as great, for although there are only half as many older as younger women in AgeX the older women who will be included in the main analyses population have thus far (in analyses blind to the treatment allocation) had about as many breast cancer deaths in total as the younger women.