Behavioural Science Messages in Breast Cancer Screening: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Behavioural Science Messages in Breast Cancer Screening (NCT05395871), a randomized na study. The primary outcome is No. of Participants Taking up Breast Cancer Screening at Three Months- Intention to Treat.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, single-masked, parallel trial sponsored by Imperial College London. Its status is completed. The listed start date is 2022-07-15 and the primary completion date is 2023-01-15. Enrollment is listed as 34047.

Three intervention groups are named: Usual Care, Behavioural Message, and Behavioural Message + Video. The usual-care text was scheduled for 7 days before and 48 hours before a booked or timed appointment. The behavioural message used content informed by previous co-design work and incorporated behavioural change techniques; it retained the usual-care message's video link. The video intervention used the behavioural text but replaced the link with a weblink to an animated video. Further detail about how the animated video was developed is not reported in the registry record.

The primary outcome is specified for people with a timed invitation and concerns screening uptake at 3 months after the initial invitation. The registry also lists outcomes concerning uptake by invitation type, sociodemographic groups, and screening history. The record does not report the allocation sequence method, the masking procedure, or which people were masked. It also does not report the original sample-size justification or detailed recruitment and follow-up procedures. The trial's listed enrollment should therefore be read as a registry-level design description, not as the denominator for each posted outcome comparison.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Timed invitation

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.

6. Primary Endpoint

The registry lists the primary outcome as No. of Participants Taking up Breast Cancer Screening at Three Months- Intention to Treat, measured over 3 months.

The primary endpoint is the number of participants taking up breast cancer screening at three months, described in the record as percentage uptake after the initial invitation letter and assessed by intention to treat. The primary population is labelled “Timed invitation.” The arm-level results express the event count against the number recorded in each arm: Usual Care had 2225 events among 3094, Behavioural Message had 2064 among 2952, and Behavioural Message + Video had 2137 among 2981.

Screening uptake is a binary outcome: each participant either took up screening during the stated follow-up period or did not. Comparing the proportion with the event makes the outcome interpretable as attendance uptake, rather than as a measure of how often a person attended. The three-month time point anchors the comparison to the initial invitation and gives the endpoint a defined observation window.

The intention-to-treat label indicates that the primary question is framed around assigned groups. The registry does not report the operational rules used to define the analysis population or handle missing outcome information. Nor does it provide further detail about how uptake was recorded. These reporting gaps limit what can be inferred about the endpoint's measurement and analysis beyond its stated definition and follow-up period.

7. Results Posted in the Registry

• Behavioural Message: 69.9% (2064/2952) versus 71.9% (2225/3094) on control; risk difference -2.0 percentage points (95% CI -4.3 to 0.3), risk ratio 0.97 (0.94–1.00); unadjusted two-proportion z-test p = 0.088.
• Behavioural Message + Video: 71.7% (2137/2981) versus 71.9% (2225/3094) on control; risk difference -0.2 percentage points (95% CI -2.5 to 2.0), risk ratio 1.00 (0.97–1.03); unadjusted two-proportion z-test p = 0.845.

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.

No. of Participants Taking up Uptake of Breast Cancer Screening, Three Months After the Initial Invitation Letter, Amongst Those Given Different Invitation Types.

• 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:
  • Behavioural Message- Open: 48.3% (3909/8095) versus 47.4% (4104/8654) on control; risk difference 0.9 percentage points (95% CI -0.6 to 2.4), risk ratio 1.02 (0.99–1.05); unadjusted two-proportion z-test p = 0.262.
  • Behavioural Message + Video- Open: 48.1% (3978/8271) versus 47.4% (4104/8654) on control; risk difference 0.7 percentage points (95% CI -0.8 to 2.2), risk ratio 1.01 (0.98–1.05); unadjusted two-proportion z-test p = 0.381.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Behavioural Message- Open and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Behavioural Message + Video- Open and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary questions about uptake by invitation type, deprivation and ethnicity, and screening history. Numerical comparisons are posted for the invitation-type outcome labelled “Open.” In those comparisons, the risk-difference estimates are positive relative to usual care, and both confidence intervals include zero. This contrasts with the negative point estimates in the primary timed-invitation comparisons, but the secondary estimates also remain uncertain and do not establish clear group differences.

The relationship between these results is descriptive rather than a direct test of whether invitation type changes the treatment effect. The primary endpoint concerns people with a timed invitation, whereas the posted secondary comparison is labelled open. The populations and outcome contexts should not be assumed to be interchangeable. Nor does a difference in the direction of point estimates establish a subgroup interaction; the record does not report a formal interaction analysis.

The registry lists secondary outcomes but does not report analyses for the specified sociodemographic or screening-history groups. The number of outcome measures is listed as 5, and 3 secondary outcomes are posted; no reported secondary analyses are listed for the broader subgroup questions. Consequently, the overall secondary pattern is limited to the available invitation-type comparisons and cannot be generalized to every listed secondary question.

Unadjusted secondary findings generally carry less weight than a prespecified primary comparison because multiple outcomes and subgroup comparisons create more opportunities for chance findings. This is a general statistical concern, not evidence that any particular result is false. The record does not report whether secondary analyses were prespecified, how many comparisons were planned, or whether multiplicity was addressed. The secondary results are best treated as additional descriptive evidence rather than independent confirmation of the primary result.

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

• No. of Participants Taking up Breast Cancer Screening, Three Months After the Initial Invitation Amongst Those From Sociodemographic Groups (Deprivation, Ethnicity)
• No. of Participants Taking up Uptake of Breast Cancer Screening, Three Months After the Initial Invitation Letter, Amongst Those Given Different Invitation Types.
• No. of Participants Taking up Breast Cancer Screening, Three Months After the Initial Invitation Letter, Amongst Those With Different Screening History

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

A risk difference subtracts the event proportion in the comparator group from the event proportion in the intervention group. It is expressed on the probability scale, so zero corresponds to equal observed proportions, a positive value means a higher observed proportion in the intervention group, and a negative value means a lower observed proportion. The primary estimates are reported as risk differences. This scale makes the direction of the contrast straightforward to read, but the estimate remains uncertain and should be interpreted alongside its confidence interval.

How should the confidence interval and p-value be read?

A confidence interval describes the uncertainty around an estimated contrast under the statistical model used. In general, a narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size and direction of the effect. For both primary comparisons, the 95% confidence interval contains zero. That means the estimates do not rule out no difference, and they also leave room for effects in either direction. The unadjusted p-values are tests of compatibility with a no-difference hypothesis under their assumptions; they are not measures of clinical importance or probabilities that the hypothesis is true.

The posted p-values are explicitly unadjusted. They do not account for any adjustment across multiple comparisons. The registry does not report a multiplicity strategy, so the estimates and p-values should not be treated as if a family-wise or other correction had been applied.

What does intention to treat mean in this record?

The primary outcome title and description identify the analysis as intention to treat. In general, an intention-to-treat approach analyses participants according to their assigned group, regardless of later adherence, and aims to preserve the randomized comparison. The record does not report how assignment and eligibility were operationalized for this analysis, how missing outcomes were handled, or whether any participants were excluded from the analysis. It is therefore not possible to assess the precise implementation of the stated approach from the registry record alone.

What can be learned from the arm counts?

The arm-level event counts and denominators describe the posted outcome data for the primary comparison. The observed proportions are also reported as p0 and p1 in the underlying calculations, but the explanatory interpretation does not require additional calculations from the counts. The analysis shown is unadjusted: no adjustment variables or adjusted effect estimates are reported. Random allocation supports a group comparison, but the registry entry alone does not establish whether the posted estimates account for any features of the study beyond the reported arm counts.

In general, adjustment can be used to account for prognostic variables or design features, but it must be specified and reported to evaluate. The registry record does not report covariates included in a model, a model specification, or adjusted estimates. The displayed risk differences should therefore be read as unadjusted comparisons rather than as adjusted causal estimates.

Why is over-dispersion not relevant to this endpoint?

Over-dispersion concerns outcomes where the observed variation exceeds what a chosen probability model expects, particularly in some count or clustered-data settings. The primary endpoint is a binary event count and the registry gives no evidence that an over-dispersion model was used or required. There is no reported model description or diagnostic information from which to evaluate over-dispersion. More generally, the choice of statistical model should follow the outcome structure and trial design; it cannot be reconstructed from the event counts alone.

The registry identifies a randomized, single-masked, parallel design, but does not report details of the randomization procedure, masking implementation, or analysis model. It also does not report interim analyses, a prespecified statistical analysis plan, or a sample-size justification. Those details should not be assumed from the design labels or the posted estimates. The sample-size planning illustrations are separate from the trial's own design rationale.

11. Confidence Intervals and Precision

Precision is about how tightly the data locate an effect estimate, rather than whether the estimate is statistically significant. For Behavioural Message versus usual care, the 95% confidence interval for the risk difference runs from -0.043 to 0.003. For Behavioural Message + Video versus usual care, it runs from -0.025 to 0.020. Both intervals include zero, so neither comparison rules out no difference. They also include values on either side of zero, leaving uncertainty about the direction of the underlying difference.

The first interval extends farther into the negative direction than the positive direction; the second extends in both directions around its point estimate. The intervals should be read in the outcome's risk-difference scale. They do not say that the true effect has a particular probability of lying within the displayed limits. In general, a confidence interval is produced by a procedure that, across repeated applications under its assumptions, has a stated coverage property.

The interval widths also indicate that the estimates do not determine a single precise effect size. They allow a range of values, including differences that may matter more or less in practice. The registry record does not specify a threshold for a meaningful change in uptake, so statistical precision cannot be translated into a judgment of practical importance from this entry alone. The unadjusted p-values add a test-based summary, but do not replace the confidence intervals or remove their uncertainty.

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 planning figures are participants per arm, not total participants across groups or total events. They are illustrations based on the observed effect, not the original trial's design assumptions; those original assumptions are not reported in the registry record. The stated illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect set to the stated fraction of the observed effect.

The 80% power column gives the estimated number of participants per arm for a future comparison to have an 80% chance of detecting the specified effect under the stated planning assumptions, if that effect is real and the assumptions hold. The 90% power column describes the corresponding planning target with a 90% chance. Higher power requires more participants when the other assumptions are held constant. Likewise, smaller effects are harder to distinguish from random variation and require more participants per arm than larger effects.

The planning values should be interpreted as conditional design illustrations, not as a claim that the completed trial had a particular probability of finding an effect. They do not establish that the original design was adequate or inadequate, because the registry record does not report the original design assumptions or sample-size justification. This is not observed power.

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 = 0.719; treatment proportion p₁ = 0.699; average p̄ = 0.709.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6423 = 1.2588.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6421 = 0.5404.
4. n = (1.2588 + 0.5404)² / (-0.0199)² = 8,136.3, rounded up to 8,137 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 <- 0.719133807369101                          # control proportion
p1 <- 0.699186991869919                          # 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(5395871)
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 = 8,137 (80% power), 10,892 (90% power)
 75% of observed effect: n per arm = 14,392 (80% power), 19,267 (90% power)
 50% of observed effect: n per arm = 32,216 (80% power), 43,127 (90% power)
power.prop.test: 8136.3 
Simulated power at n = 8,137 per arm: 0.797 (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

Multiplicity arises when several outcomes, groups, or comparisons are examined. With more statistical tests, the chance of at least one apparently unusual result can increase, even if there is no true effect. The record identifies one primary endpoint and lists secondary questions involving invitation type, deprivation, ethnicity, and screening history. It does not report a multiplicity adjustment, a hierarchy among the secondary outcomes, or a statistical analysis plan describing how these questions were to be interpreted. The posted secondary p-values are unadjusted.

The registry does not report interim analyses or stopping rules, so their use cannot be inferred. It also does not report a sample-size justification for the trial's original design. The planning illustrations based on observed effects do not fill that gap and should not be read as evidence of the design rationale.

The primary outcome is labelled intention to treat, but the operational analysis population is not described in detail. The record does not report how missing outcome data were handled, whether any participants were excluded from the primary analysis, or whether a sensitivity analysis assessed the impact of missingness. It also does not report adherence or crossover information. These omissions prevent assessment of how closely the analysis followed the stated intention-to-treat label.

Randomization and masking are identified at a high level, but the record does not describe sequence generation, allocation concealment, who was masked, or how masking was maintained. Those details can matter when assessing risk of bias. Their absence from the registry entry does not establish that methods were inadequate; it means they cannot be evaluated from the record.

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 records zero serious adverse events, zero other adverse events, and zero deaths in each of the three listed groups. The serious-event and other-event at-risk counts are listed as 11748 for Usual Care, 11047 for Behavioural Message, and 11252 for Behavioural Message + Video. The figures are presented as recorded in the registry and should not be added together or treated as denominators for the primary uptake comparison.

Zero recorded events means that none were entered in these outcome fields; it does not by itself establish that no events occurred or that the interventions have no safety concerns. The registry record does not report how adverse events were collected, the observation period for safety, or definitions and ascertainment procedures. It also lists no serious adverse-event terms. These data therefore describe the posted safety fields, with limited information about their completeness or context.

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

The primary results show that observed screening uptake was lower in the Behavioural Message arm than in Usual Care by the estimated risk difference of -0.020, while the Behavioural Message + Video estimate was -0.002. Both 95% confidence intervals include zero. The data therefore do not establish a clear difference in uptake between either behavioural approach and usual care for the specified timed-invitation population and three-month outcome.

This interpretation is not the same as concluding that the interventions are equivalent, or that they have no effect. The confidence intervals allow for differences in either direction, and the record does not provide a threshold for a practically important change. A failure to establish a clear difference does not prove that all relevant effects are absent. The registry results also do not establish that one active intervention is better than the other, because a direct comparison between the active approaches is not reported.

The finding applies to the posted primary outcome and its defined setting. It should not automatically be extended to other invitation types, screening histories, or sociodemographic groups. Although the record lists secondary questions in those areas, analyses are not reported for all of them. The secondary invitation-type comparisons likewise do not provide a definitive basis for generalizing the primary result to a different invitation context.

Interpretation is further limited by unreported details about missing data, analysis methods, multiplicity, and the original sample-size rationale. These are reporting limitations, not proof that the trial was conducted improperly. The registry entry supports a careful description of the recorded estimates and their uncertainty, but not broader claims about screening policy or effects beyond the population and outcome specified.

17. Why This Trial Matters Statistically

This trial addresses a practical statistical question: whether changing the content or format of screening reminders is associated with different uptake after an invitation. Its three-arm randomized parallel design allows the behavioural message and the message paired with an animated video to be compared with usual care. The primary outcome is a clearly timed binary event, which makes the target contrast understandable as a difference in uptake proportions.

The estimates also illustrate why a point estimate alone is not enough. The primary contrasts are negative, but their confidence intervals include zero and cover effects in either direction. Reporting both the estimated difference and its uncertainty gives a more informative account than classifying results only by a p-value. The observed evidence does not establish a clear difference, while also leaving uncertainty about the effect sizes compatible with the data.

The record shows the value of separating a primary question from secondary questions. The primary outcome concerns timed invitations; secondary questions address other invitation or participant characteristics. Those questions may be relevant, but their interpretation depends on adequate reporting of prespecification, analysis methods, and multiplicity. Here, those details are not reported in the registry record, which limits the weight that can be placed on secondary findings.

Finally, the planning illustrations demonstrate how assumptions about the effect to detect shape sample-size requirements. They are not a substitute for the missing original design rationale. Separating planning calculations from trial results helps readers distinguish prospective design choices from retrospective illustrations based on observed estimates.

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.

The registry record does not describe the randomization sequence, allocation concealment, or implementation of the stated single masking. It does not identify who was masked. These omissions limit assessment of potential bias, although they do not show that bias occurred.

The primary endpoint is labelled intention to treat, but the record does not give the operational analysis-population definition, missing-data approach, or sensitivity analyses. No adjusted estimates or model specification are reported. The displayed comparisons are unadjusted, and the record does not explain whether additional design features were considered in the analysis.

Several outcome and subgroup questions are listed, but analyses are not reported for all of them. Multiplicity handling, prespecification of the secondary analyses, and interim-analysis procedures are not reported. The original sample-size justification is also not reported, so the planning illustrations based on observed effects cannot establish whether the original study was designed around a particular target effect.

The primary result is limited to the timed-invitation population and the three-month uptake endpoint. The registry does not provide enough detail to assess how screening uptake was ascertained or how missing outcome information might affect the estimates. Safety fields list zero events, but collection methods and observation periods are not described. These limitations constrain interpretation of the registry results; they should not be mistaken for evidence that unreported procedures were absent or inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Behavioural Science Messages in Breast Cancer Screening — NCT05395871.
• Registry record last updated 2025-01-30; status last verified 2025-01.
• Results first posted 2025-01-30.
• 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

NCT05395871 is a completed, randomized, single-masked, parallel trial sponsored by Imperial College London. It compared usual-care text reminders with a behavioural message and a behavioural message paired with an animated video. The primary question concerned breast cancer screening uptake at 3 months among people with a timed invitation, with the outcome labelled intention to treat.

The primary risk-difference estimates were -0.020 for Behavioural Message versus usual care and -0.002 for Behavioural Message + Video versus usual care. Both confidence intervals included zero, and the registry results do not establish a clear difference in uptake. Secondary invitation-type comparisons were also uncertain; analyses for the listed sociodemographic and screening-history questions are not reported. The registry does not report the original sample-size rationale, detailed analysis plan, multiplicity approach, or missing-data handling.