The Digital Breast Tomosynthesis Trial in Bergen: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Digital Breast Tomosynthesis Trial in Bergen (NCT02835625), a randomized na study. The primary outcome is Number of Participants With Screen-Detected Breast Cancer.

2. Clinical Question

The question concerns screening performance in the specified program and age group, rather than treatment after a cancer diagnosis. Screen-detected cancer is an observed event during screening; it does not, by itself, describe all cancers that may arise over time or establish the effect of screening on later health outcomes. The registry also lists interval breast cancer as a secondary outcome, which captures a different part of the screening picture. The primary comparison therefore needs to be read alongside the recall and interval-cancer results, while keeping each endpoint’s definition and observation period in view.

3. Trial Design

The Digital Breast Tomosynthesis Trial in Bergen was a randomized, parallel-group trial with no masking reported. Its registry status is completed. The listed start is 2016-01, and primary completion is 2018-06. Enrollment is recorded as 29453. The registry identifies the Norwegian Institute of Public Health as sponsor and lists Breast Neoplasms as the condition.

Eligible participants were described as women aged 50-69 years invited to the Norwegian Breast Cancer Screening Program at the screening unit in Bergen, Norway. The trial compared synthetic mammography plus digital breast tomosynthesis with digital mammography. The intervention descriptions indicate independent image reading by two radiologists in each arm and a consensus meeting to decide whether to recall. For SM+DBT, women selected for further assessment after a positive screening exam were to be recalled. The record does not describe masking, and the trial is explicitly listed as unmasked.

The primary outcome was the number of participants with screen-detected breast cancer, assessed over 36 months from start up of the trial. Secondary outcomes listed by the registry include screen-detected cancers among participants recalled for further assessment, recalls due to mammographic findings, incremental screening costs, prognostic and predictive tumor characteristics, and interval breast cancer. A 60-month timeframe is listed for interval breast cancer. Results are posted for several, but not all, of these secondary topics.

The registry record does not report the original sample-size justification, the randomization procedure, allocation concealment, eligibility criteria beyond the described population, or detailed follow-up and participant-flow information. It also does not report the trial’s full statistical analysis plan or analysis populations. These omissions limit how fully the reported comparisons can be connected to the planned design.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Women that attended screening but had breast implant were not invited to participate, and thus not randomized to either of the study groups.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: We excluded women with previous breast cancer (DBT = 314, DM = 316), women with breast symptoms at screening (DBT = 39, DM = 34) and one woman with metastasis from melanoma (DBT).

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Screen-Detected Breast Cancer, measured over 36 months from start up of the trial.

The primary endpoint is the number of participants with screen-detected breast cancer. The registry describes the purpose as comparing rates of screen-detected breast cancer between tomosynthesis and digital mammography in a population-based screening program. The listed timeframe is 36 months from start up of the trial.

This endpoint measures cancers identified through screening during the specified period. It is relevant to screening performance because the two approaches may differ in what is detected during screening. However, a count of screen-detected cancers does not alone describe the balance of benefits and burdens, nor does it establish whether detection changes later outcomes. Recall and follow-up outcomes help characterize the process surrounding a positive screen, while interval cancers address cancers recorded between screening detection and later follow-up. Those outcomes answer related but distinct questions and should not be treated as interchangeable with the primary endpoint.

The registry reports 95 screen-detected breast cancers among 14380 participants in the SM+DBT arm and 87 among 14370 in the DM arm. The posted comparison gives a risk-difference estimate of -0.001, with an interval from -0.002 to 0.001 and an unadjusted p-value of 0.555. The estimate is close to zero relative to the scale of the risk, and the interval includes zero. These data describe the recorded endpoint; they do not establish that the approaches are equivalent or that either has a particular effect on outcomes beyond screening detection.

7. Results Posted in the Registry

• Digital Mammography: 0.6% (87/14369) versus 0.7% (95/14380) on control; risk difference -0.1 percentage points (95% CI -0.2 to 0.1), risk ratio 0.92 (0.69–1.22); unadjusted two-proportion z-test p = 0.555.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number and Percentage of Participants Screen-Detected Breast Cancer Among Participants Recalled for Further Assesment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Digital Mammography: 15.2% (87/571) versus 21.4% (95/444) on control; risk difference -6.2 percentage points (95% CI -11.0 to -1.3), risk ratio 0.71 (0.55–0.93); unadjusted two-proportion z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Digital Mammography than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Recalled for Further Assesment Due to Mammographic Findings

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Digital Mammography: 4.0% (571/14369) versus 3.1% (444/14380) on control; risk difference 0.9 percentage points (95% CI 0.5 to 1.3), risk ratio 1.29 (1.14–1.45); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Digital Mammography than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Interval Breast Cancer

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Digital Mammography: 0.2% (29/14369) versus 0.1% (20/14380) on control; risk difference 0.1 percentage points (95% CI -0.0 to 0.2), risk ratio 1.45 (0.82–2.56); unadjusted two-proportion z-test p = 0.197.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Digital Mammography and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the interpretation beyond the number of screen-detected cancers in the full randomized groups. They include recall, screen-detected cancers among recalled participants, and interval cancers, along with registry-listed outcomes on cost and tumor characteristics. These endpoints describe different steps or consequences of screening and use different denominators and, in one case, a longer observation period. They should not be combined mentally into a single overall treatment effect.

Across the secondary results with posted comparisons, the pattern is not uniform across endpoints. Some comparisons show a clearer difference in the screening process or in the selected group referred for further assessment, while the interval-cancer comparison is less conclusive. This can coexist with the primary result, because a screening approach may affect recalls and the composition of those recalled without producing a clearly different count of screen-detected cancers across all participants. The primary and secondary endpoints therefore answer related but distinct questions.

The result among recalled participants is conditional on being recalled. This subgroup is defined after the screening result and is not interchangeable with the randomized population. A difference within that selected group does not by itself establish a difference in overall screening performance. Similarly, recall frequency reflects a process measure, while interval cancer addresses cancers recorded over a later period. Their interpretation depends on the specific endpoint definition and follow-up timeframe.

The registry lists five secondary outcomes, but results for incremental costs and prognostic and predictive tumor characteristics are not reported in the registry record. The posted secondary comparisons also have unadjusted p-values. When several outcomes are examined, an unadjusted result carries less weight as confirmatory evidence because the chance of at least one apparently notable result can increase across repeated testing. The registry record does not report a multiplicity adjustment or identify a prespecified hierarchy for secondary outcomes. These results are best treated as supporting and exploratory evidence alongside, rather than replacements for, the primary comparison.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number and Percentage of Participants Screen-Detected Breast Cancer Among Participants Recalled for Further Assesment
• Number of Participants Recalled for Further Assesment Due to Mammographic Findings
• Incremental Costs of Screening With Tomosynthesis Versus Digital Mammography
• Prognostic and Predictive Tumor Characteristics for Screen-Detected Breast Cancer
• Number of Participants With Interval Breast Cancer

9. Statistical Interpretation

10. Statistical Methods Explained

These results compare counts of participants with an event between two randomized arms. The primary endpoint is binary at the participant level: a participant either had screen-detected breast cancer recorded during the stated period or did not. A count is reported for each arm, alongside the number of participants in that arm. The corresponding event proportions give the counts in relation to their arm denominators. The registry record does not report a more detailed account of how missing outcome data or incomplete follow-up were handled.

What does the risk difference express?

A risk difference is the difference between event proportions on the probability scale. A value of zero corresponds to equal proportions; positive and negative values indicate direction according to the ordering used for the comparison. For the primary endpoint, the posted estimate is -0.001, with an interval from -0.002 to 0.001. The listed arm proportions are 0.007 for SM+DBT and 0.006 for DM. Because the interval includes zero, the data do not rule out no difference under the method used to construct that interval. The registry record does not state the confidence level or the calculation method for the interval.

How do relative measures differ?

A risk ratio compares event proportions by division, while an odds ratio compares event odds. A value of 1 represents no relative difference. For the primary endpoint, the posted risk ratio is 0.916, with an interval from 0.686 to 1.225, and the posted odds ratio is 0.916, with an interval from 0.684 to 1.226. These are alternative scales for expressing the comparison, not independent confirmations. With uncommon events, odds and risks can be numerically similar, but they remain distinct measures. The intervals spanning 1 indicate that these posted relative estimates also allow no association as well as effects in either direction.

What does the p-value contribute?

A p-value describes how unusual a test statistic at least as extreme as the observed one would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The primary unadjusted p-value is 0.555. Read together with the estimate and interval, it indicates that the posted comparison does not provide strong statistical evidence against a null of no difference. It does not show that there is no difference. The registry record does not report the test procedure underlying the p-value, beyond its unadjusted status.

What does unadjusted mean?

An unadjusted comparison uses the reported arm summaries without accounting for covariates or other adjustments. Randomization can help make groups comparable on average, but it does not make adjustment irrelevant in every analysis. The record does not report a covariate-adjusted primary estimate, a model specification, or the reason for choosing the posted comparison. The posted results should therefore be understood as simple arm-level comparisons, not as estimates adjusted for participant characteristics or other factors.

Why consider the denominator and endpoint definition?

The denominator determines the group to which an event proportion applies. The primary endpoint uses the arm participant counts reported with the screen-detected cancer counts. A secondary result among participants recalled for further assessment has a different denominator and answers a conditional question about those recalled. A recall outcome instead uses all participants in the screening arms as its denominator. These distinctions matter: conditional results among recalled participants cannot be read as if they were risks among everyone randomized. The registry record does not provide additional detail about whether all participants had complete ascertainment for every outcome.

What are the limits of the posted analysis information?

The registry lists no reported analyses in its analysis field. It does provide counts and comparison estimates, but the original analysis plan, model choices, missing-data methods, analysis populations, interim analyses, and handling of protocol deviations are not reported in the registry record. The primary outcome is a count of participants with an event, not a time-to-event estimate. The registry does not describe an analysis of time until cancer detection. The statistical interpretation should stay close to the posted endpoint, observed counts, intervals, and unadjusted p-values, rather than assuming methods that are not documented.

General statistical principle: confidence intervals communicate uncertainty about an estimate under the method used to construct them. Their width reflects both the amount of information and the variability relevant to the endpoint. A range that includes the null value indicates that the data are compatible with that value at the interval’s stated confidence level, but the confidence level and construction method are not reported in the registry record. General statistical principle: a non-significant result is not a demonstration of equivalence. Establishing equivalence requires a prespecified margin and a suitable analysis; those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.001, with an interval from -0.002 to 0.001. Its lower and upper limits fall on opposite sides of zero. Thus the posted interval includes no difference and also permits a difference in either direction. The estimate is not precise enough to distinguish those possibilities. The registry record does not state the confidence level or method used for the interval, so the interval should be read as posted rather than assigned an unstated level.

The relative-effect intervals also include their null value of 1: the risk ratio is 0.916, with an interval from 0.686 to 1.225, and the odds ratio is 0.916, with an interval from 0.684 to 1.226. These ranges are broad relative to their point estimates. They do not support a precise claim about the direction or magnitude of a relative difference. The p-value of 0.555 is consistent with the lack of clear evidence against no difference, but it does not resolve the uncertainty represented by the intervals.

General statistical principle: an interval is useful because it shows a range of effect values compatible with the observed data and the interval procedure, rather than presenting only a single point estimate. It is not a guarantee that the true effect lies within the particular realized range. Precision also depends on the event frequency and variability, not only on the overall number of participants. Here, the primary event counts are modest compared with the arm denominators, and the estimated difference is close to zero. These features help explain why a point estimate alone should not be read as a definitive answer.

For interpretation, the key distinction is between absence of clear evidence for a difference and evidence that differences are negligible. The primary interval crosses zero, but no equivalence margin is reported. Without a specified margin and a corresponding design and analysis, the result cannot establish equivalence. The interval also does not describe uncertainty in outcomes that were not reported, such as cost or tumor characteristics. Precision is endpoint-specific and should not be transferred from one outcome to another.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s own design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets the stated fraction of the observed effect. The trial’s original sample-size assumptions are not reported in the registry record.

For the primary binary outcome, the figures are participants per arm, not total participants and not total events. The 80% power column means the number of participants per arm estimated to give an 80% chance of detecting the target effect under the listed assumptions if that effect were the true one. The 90% column uses a higher chance of detection and therefore requires more participants per arm for the same target effect. For the scenario using 100% of the observed effect, the illustration gives 324,429 participants per arm for 80% power and 434,317 participants per arm for 90% power. The table also considers planning for 75% and 50% of the observed effect.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The values can be used to understand how assumptions about the target effect influence planning, but they are not a description of the trial’s achieved power. This is not observed power. They also do not establish what enrollment would be appropriate for a future study, because the illustration depends on its assumptions and does not incorporate unreported design features.

The sample-size values are computed separately for each outcome and use the observed comparison as their reference. Rare outcomes can lead to very large planning figures under this approach. The planning table should therefore be read as an illustration of statistical sensitivity to the assumed effect size, not as a recommendation or a retrospective judgment of the trial’s design.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.007; treatment proportion p₁ = 0.006; average p̄ = 0.006.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1122 = 0.2198.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1122 = 0.0944.
4. n = (0.2198 + 0.0944)² / (-0.0006)² = 324,428.3, rounded up to 324,429 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.00660639777468707                          # control proportion
p1 <- 0.00605470109262997                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2835625)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 324,429 (80% power), 434,317 (90% power)
 75% of observed effect: n per arm = 583,005 (80% power), 780,478 (90% power)
 50% of observed effect: n per arm = 1,325,807 (80% power), 1,774,878 (90% power)
power.prop.test: 324428.3 
Simulated power at n = 324,429 per arm: 0.795 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes in addition to the primary endpoint. The posted secondary comparisons include outcomes related to cancers among recalled participants, recalls due to mammographic findings, and interval breast cancer. Costs and tumor characteristics are also listed, but their results are not reported in the registry record. Examining several outcomes raises a multiplicity issue: if each is tested separately without adjustment, the chance of at least one result appearing statistically notable can be higher than for a single planned test.

The posted secondary p-values are unadjusted. The registry record does not report whether a formal multiplicity procedure was used, whether outcomes were ordered in a testing hierarchy, or which secondary outcomes were designated as confirmatory. Therefore, an isolated secondary p-value should not be interpreted as having the same evidential weight as a primary endpoint result from a prespecified testing plan. The record also does not report a statistical analysis plan that would clarify endpoint prioritization or the handling of multiple comparisons.

Details about missing data and analysis populations are also not reported in the registry record. It does not specify whether analyses followed intention-to-treat principles, how participants with incomplete screening or follow-up were handled, or whether imputation or sensitivity analyses were used. These omissions matter because missing outcome information can affect event counts and the denominators used for comparisons. The posted arm counts do not, by themselves, establish how missingness was handled.

The record lists no reported analyses in its analysis field, and it does not describe interim analyses, stopping rules, or protocol deviations. This does not establish that such procedures were absent; it means their details are not reported in the registry record. Without those details, the safest interpretation is to describe the posted estimates and their uncertainty while avoiding assumptions about analysis populations, multiplicity control, or missing-data methods.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse events affecting 0 participants in the SM+DBT safety group, with 14734 at risk, and 0 in the DM safety group, with 14719 at risk. It also reports 0 other adverse events in each group. Deaths are listed as 2 in each group. These figures describe the recorded safety entries; they do not show whether a death was caused by, related to, or unrelated to the screening procedure. Cause, timing, and relatedness are not reported in the registry record.

The safety denominators differ from the participant denominators listed for the primary outcome. The registry does not explain that difference, so the safety and efficacy counts should not be treated as if they necessarily use the same analysis population. A zero count in a reported category does not prove that the underlying risk is zero; it means no events in that category were recorded in the posted result. The registry record does not provide detailed event descriptions or serious adverse event terms.

These limited entries do not permit a comprehensive comparison of safety. They should be read as registry-reported counts, without inferring causation or broader safety conclusions from the absence of recorded events in the listed categories.

16. What the Result Does, and Does Not, Mean

The primary result describes screen-detected breast cancer recorded during the specified timeframe in the two randomized screening groups. The posted point estimate is close to zero, and its interval includes zero. The associated unadjusted p-value is 0.555. Taken together, these statistics do not provide clear evidence of a difference in the primary endpoint, but they do not prove that the screening approaches are identical.

The result is specific to the trial’s population and setting: women aged 50-69 years invited to the Norwegian Breast Cancer Screening Program at the screening unit in Bergen, Norway. It is also specific to the outcome definition and the listed timeframe of 36 months from start up of the trial. The registry result does not answer every question about screening. In particular, it does not by itself establish effects on long-term health outcomes, the balance of benefits and harms, or cost-effectiveness. Although the registry lists cost and tumor-characteristic outcomes, results for those topics are not reported in the registry record.

The secondary outcomes help describe parts of the screening pathway, such as recall and interval cancer, but they do not replace the primary result. Some secondary comparisons are conditional on recall and therefore concern a selected group rather than all participants. Their unadjusted p-values and the absence of a reported multiplicity plan also limit their confirmatory weight.

General statistical principle: a result that does not cross a conventional threshold for statistical significance is not evidence of no effect. A claim of equivalence would require a prespecified margin and analysis, which are not reported in the registry record. The most defensible conclusion is narrower: the posted data show similar observed primary event proportions, with uncertainty that allows differences in either direction. They do not settle whether any difference is important in practice, nor do they support medical advice about which screening approach an individual should choose.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares two screening approaches in a randomized, parallel-group setting within a population-based program. Random allocation is intended to support a fair comparison of groups, and the registry reports the number of participants and screen-detected cancers in each arm. The result also illustrates why counts, proportions, effect estimates, and uncertainty need to be considered together. The primary point estimate alone would conceal the range of differences compatible with the data.

The endpoint structure is important. Screen-detected cancers, recalls, cancers among recalled participants, and interval cancers capture different aspects of screening. A single endpoint cannot fully summarize those processes. The trial’s secondary results show why a broad statistical reading must distinguish overall randomized-group comparisons from outcomes restricted to participants who were recalled. The different timeframes also matter: the primary outcome is listed at 36 months from start up, while interval cancer is listed at 60 months from start up.

The record also provides an example of the limits of registry reporting. It includes several outcome counts and comparison estimates, but does not report the original design assumptions, detailed analysis plan, missing-data methods, multiplicity handling, or results for every listed outcome. Those omissions do not invalidate the posted results, but they limit the ability to assess how completely the results follow the original plan and how secondary evidence should be weighted.

Finally, the planning illustrations show how strongly sample-size requirements depend on the effect a future study aims to detect. The values are illustrative and should not be mistaken for the design rationale of this completed trial. This distinction between a retrospective calculation and the original design is central to responsible interpretation of power and precision.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to the registry record constrain interpretation. The original sample-size justification and design assumptions are not reported, so the trial’s planned target effect and power cannot be evaluated from the record. The posted sample-size illustration is based on the observed effect and a stated set of planning assumptions; it is not evidence about the original design.

The statistical analysis plan is not reported. The record does not specify the analysis population, covariate adjustments, missing-data handling, interval estimation method, or the procedure used for the p-values. It also does not report whether multiplicity was controlled, whether interim analyses occurred, or how protocol deviations were addressed. These details affect the strength and scope of conclusions that can be drawn, particularly for secondary outcomes.

The registry reports randomized assignment and no masking, and it describes independent reading by two radiologists followed by consensus. It does not provide additional information about allocation concealment, reader training, adherence to the assigned screening method, participant flow, or completeness of follow-up. The safety denominators differ from those listed for the primary endpoint, without an explanation in the registry record.

Not all registry-listed outcomes have posted results. Incremental costs and prognostic and predictive tumor characteristics are listed, but their results are not reported in the registry record. The posted evidence therefore does not support conclusions about cost-effectiveness or those tumor characteristics. The primary outcome is also a screening-detection measure and should not be treated as a direct measure of long-term health outcomes. These limitations favor a focused interpretation of the available endpoint estimates rather than broad claims about screening overall.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Digital Breast Tomosynthesis Trial in Bergen — NCT02835625.
• Registry record last updated 2024-08-28; status last verified 2020-01.
• Results first posted 2021-01-15.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized, unmasked, parallel-group trial in Bergen comparing synthetic mammography plus digital breast tomosynthesis with digital mammography among women aged 50-69 years invited to a population-based screening program. Enrollment is recorded as 29453. The primary endpoint was the number of participants with screen-detected breast cancer over 36 months from start up of the trial.

The posted primary counts were 95 among 14380 participants in the SM+DBT arm and 87 among 14370 in the DM arm. The risk-difference estimate was -0.001, with an interval from -0.002 to 0.001, and the unadjusted p-value was 0.555. This comparison does not provide clear evidence of a difference, while its interval remains compatible with differences in either direction.

Secondary outcomes add information on recall and interval cancer, but results are not reported for every outcome listed in the registry. The record does not report the original sample-size justification, detailed statistical plan, analysis populations, missing-data methods, or multiplicity handling. Consequently, conclusions should remain limited to the posted results and their stated uncertainty.