A Randomized Trial of Letters From Family Physicians to Encourage Screening Mammography in Overdue Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Randomized Trial of Letters From Family Physicians to Encourage Screening Mammography in Overdue Women (NCT02660788), a randomized na study. The primary outcome is Percentage of Overdue Women Returning for Screening Mammography.

2. Clinical Question

The clinical question is whether adding a family-physician-signed letter to the existing reminder postcard is associated with a different return rate among women overdue for screening. The registry describes an organized, publicly funded screening program in British Columbia, where screening mammography is recommended at 24-month intervals. Women were identified as overdue in the program database, and family physicians were recruited by mail and asked to sign letters to overdue women in their practices.

The comparison is between two mailed reminder strategies, not between a reminder and no reminder: both groups received the standard postcard. The intervention group also received the signed letter. The primary outcome was attendance for screening mammography, measured from randomization and assessed at 6 months. The registry results report a higher percentage returning in the family physician reminder letter arm than in the control arm. The posted estimate and its uncertainty describe this randomized comparison; they do not by themselves establish how the result would apply to other screening systems, populations, or reminder approaches.

3. Trial Design

The registry describes a randomized, double-blinded, parallel-group study conducted in British Columbia. It is listed as completed, with enrollment of 5498. The listed phase is NA. The sponsor is the British Columbia Cancer Agency. The recorded start is 2013-02, and primary completion is recorded as 2013-12.

Eligible women were aged 51-73 years and overdue for screening mammography by 6-24 months. They were identified from the database of the Screening Mammography Program of BC. The brief summary describes the program as publicly funded and organized, with screening recommended at 24-month intervals. Family physicians were recruited by mail and asked to sign letters addressed to overdue women in their practices. The women were then randomized to receive either the standard reminder postcard alone or that postcard together with a letter signed by their family physician.

The registry labels the allocation randomized, the masking double, and the model parallel. The record does not describe who was masked, how masking was maintained, or whether recipients could distinguish the reminder materials. Those details are not reported in the registry record. The arm descriptions identify mailing as the intervention delivery method. No additional information about implementation, adherence, or receipt of the mailed materials is reported in the registry record.

The outcome measure was the percentage of overdue women returning for screening mammography. Its stated timeframe was 6 months, measured from randomization. The registry reports one outcome measure and no posted secondary outcomes. The design therefore supports interpretation of the reported result as a comparison of assigned reminder strategies for the stated outcome and follow-up timeframe. Details of the trial’s original sample-size justification, statistical analysis plan, and operational procedures beyond those are not reported in the registry record.

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: Only screenees who had not had a mammogram between identification of potential participants and randomization were randomized.

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: Total includes patients who were screened before randomization

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Overdue Women Returning for Screening Mammography, measured over 6 months.

The primary endpoint was the percentage of overdue women returning for screening mammography within 6 months, measured from the date of randomization. In statistical terms, this is a binary outcome for each participant: the record counts whether a woman returned for screening within the stated timeframe or did not. The reported group percentage expresses the share with the event, rather than the timing of attendance or the number of mammograms.

This endpoint directly represents the behavior the reminder strategies were intended to encourage: attendance for a screening mammogram. It is therefore a practical outcome for comparing mailed reminder approaches in this study. Because the endpoint is defined over a fixed follow-up period, the comparison concerns whether a return occurred by that point; the registry does not report a time-to-attendance analysis.

The posted percentages were 24.0 in the control arm and 34.4 in the family physician reminder letter arm. The registry also reports a risk difference and relative measures for the comparison. The primary endpoint does not measure cancer diagnoses, later health outcomes, or the quality of screening. Those outcomes are not reported in the registry record. The endpoint should consequently be read as a measure of return for screening within the specified timeframe, not as evidence about outcomes beyond attendance.

7. Results Posted in the Registry

• Family Physician Reminder Letter Arm: 34.4% (946/2749) versus 24.0% (660/2749) on control; risk difference 10.4 percentage points (95% CI 8.0 to 12.8), risk ratio 1.43 (1.32–1.56); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The outcome is binary: for each woman, return for screening mammography within 6 months is either recorded as having occurred or not. A percentage summarizes the proportion with the event in each arm. The registry reports percentages of 24.0 for the control arm and 34.4 for the family physician reminder letter arm. These are arm-level summaries and do not show when within the follow-up period attendance occurred.

What does the risk difference express?

The risk difference compares the event probability in one arm with the event probability in the other, by subtraction. It stays on the absolute probability scale, so it describes the separation between the groups’ return rates rather than a proportional change. The registry reports a risk difference of 0.104 for the family physician reminder letter arm relative to the control arm. The associated confidence interval is reported with a lower endpoint above zero and an upper endpoint above zero. The interval method is not reported in the registry record.

How do relative risk and odds ratio differ?

The relative risk compares the probability of the event between arms as a ratio. The posted relative risk is 1.433, with a confidence interval from 1.318 to 1.559. The odds ratio compares the odds of the event rather than the probabilities; its posted value is 1.661, with a confidence interval from 1.476 to 1.868. Both are relative measures, but the odds ratio is not the same quantity as the relative risk. When an outcome is not rare, the numerical values of these measures can differ appreciably. In general, the choice of scale affects how an effect is described; it does not change the underlying group data.

What does the p-value address?

The reported p-value is <0.001. In general, a p-value evaluates how surprising data at least as incompatible with a null hypothesis would be if that null hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The registry does not report the statistical test, whether the comparison was adjusted, or the complete analysis plan. It is therefore appropriate to describe the posted p-value without assigning an unreported method to it.

Why does randomization matter?

Random allocation is intended to make treatment assignment independent of participant characteristics, on average, supporting a fair comparison between assigned groups. In this trial, the groups were assigned to the standard postcard alone or the postcard plus a letter signed by the family physician. Randomization strengthens the interpretation of a between-arm difference as a comparison of the assigned reminder strategies, subject to the conduct of the study and outcome ascertainment. It does not guarantee perfect balance in every characteristic, and the registry does not provide baseline characteristics or details of allocation implementation.

What details are not available?

The registry lists the study as double-blinded, but does not explain who was masked or how blinding was maintained. It does not describe the statistical analysis method, any adjustment variables, an interim-analysis plan, or the original sample-size calculation. Missing-data procedures, participant-level analysis populations, and protocol deviations are also not reported in the registry record. These omissions matter because they prevent readers from checking whether the posted comparison follows a prespecified analysis or how the analysis handled incomplete outcome information. No adjustment or imputation should be assumed.

In general, a confidence interval represents uncertainty around an estimate under the method used to calculate it. Its interpretation depends on that method and its assumptions. The comparison is also based on a single posted primary outcome; because no secondary outcomes are posted, the registry does not permit assessment of a broader set of outcome results or how multiplicity was handled across such a set.

10. Confidence Intervals and Precision

The registry reports the risk difference as 0.104. Its confidence interval has both endpoints above zero, indicating that the interval’s values are on the side favoring a higher return probability in the family physician reminder letter arm. The exact risk-difference endpoints are not repeated because the registry’s recorded values contain more than 3 decimal places. The interval’s width represents uncertainty around the point estimate, under the interval method and assumptions; those details are not reported in the registry record.

The relative risk estimate is 1.433, with a confidence interval from 1.318 to 1.559. The odds ratio is 1.661, with a confidence interval from 1.476 to 1.868. These intervals likewise remain above their respective null values. They describe uncertainty on different scales, and their bounds should not be compared as if they were measuring the same quantity. The registry does not report confidence intervals for the individual arm percentages.

A confidence interval is not a range guaranteed to contain the true effect, nor does it capture every source of uncertainty. In general, it reflects sampling uncertainty under a specified statistical procedure. Precision also depends on the design, the outcome data, and the method used. Because the analysis method, missing-data handling, and other relevant analytic details are not reported in the registry record, the posted intervals can be interpreted as the registry’s estimates of uncertainty, but not independently evaluated from the available description.

11. 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 events. They are illustrations based on the observed effect, not a report of the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For planning for 100% of the observed effect, the figures are 299 participants per arm for 80% power and 400 participants per arm for 90% power. For planning for 75% of the observed effect, they are 518 participants per arm for 80% power and 693 participants per arm for 90% power. For planning for 50% of the observed effect, they are 1,132 participants per arm for 80% power and 1,515 participants per arm for 90% power.

In plain language, the 80% power column gives the illustrative number per arm for a study with an 80% chance of detecting the specified effect under the listed assumptions, if that effect is real and the assumptions hold. The 90% power column uses the corresponding higher target chance. Smaller effects need more participants to distinguish them from random variation under otherwise similar assumptions, which is why the figures increase as the planned fraction of the observed effect decreases. These are planning illustrations, not observed power.

12. 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 = 0.240; treatment proportion p₁ = 0.344; average p̄ = 0.292.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6431 = 1.2604.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6389 = 0.5377.
4. n = (1.2604 + 0.5377)² / (0.1040)² = 298.7, rounded up to 299 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 <- 0.240087304474354                          # control proportion
p1 <- 0.344125136413241                          # 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(2660788)
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 = 299 (80% power), 400 (90% power)
 75% of observed effect: n per arm = 518 (80% power), 693 (90% power)
 50% of observed effect: n per arm = 1,132 (80% power), 1,515 (90% power)
power.prop.test: 298.7 
Simulated power at n = 299 per arm: 0.805 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry reports one outcome measure, the primary percentage returning for screening mammography within 6 months, and no posted secondary outcomes. It lists no analyses. This record therefore does not describe a set of multiple posted outcome tests for which a multiplicity adjustment can be evaluated. Whether the trial protocol included additional planned outcomes, subgroup analyses, or other comparisons is not reported in the registry record.

The registry does not report a multiplicity strategy, such as a prespecified hierarchy or adjustment across several tests. That absence should not be interpreted as evidence that no such strategy existed; it means the registry record does not document one. The posted p-value applies to the stated comparison, but the record does not provide enough detail to assess how it fits within any broader analysis plan.

Missing outcome data, withdrawals, exclusions after randomization, and the handling of incomplete follow-up are not reported in the registry record. The record also does not state whether analyses followed intention-to-treat principles, whether participants were analyzed according to assigned group, or whether another analysis population was used. Without those details, the completeness of outcome ascertainment and the precise population represented by the posted percentages cannot be assessed from the registry alone.

Baseline characteristics and protocol deviations are also not reported. These details can help readers evaluate the groups’ comparability and the conduct of a randomized trial, but their absence from the registry does not establish that a problem occurred. The statistical analysis plan, model specification, handling of missing data, and any interim analyses are not reported in the registry record, so no particular procedures should be inferred.

14. Safety Results

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

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 in the control arm and zero in the family physician reminder letter arm. It also records zero other adverse events in both arms. The adverse-event sections list 2749 at risk in each arm for serious events and for other events. Death counts are not reported in the registry record.

These entries describe what is posted in the adverse-event record; they do not establish that every possible event was collected or that none occurred outside the registry’s reporting process. Definitions of serious and other adverse events, collection procedures, event attribution, and the observation period are not described in the record. The absence of posted event counts does not by itself establish that the interventions are risk-free.

The study compared mailed reminder strategies, with the family physician letter added to a standard postcard in one arm. The registry’s adverse-event entries should be read separately from the primary attendance outcome. They do not provide a broader safety assessment or information about outcomes that were not reported.

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

The posted result describes a difference in the proportion returning for screening mammography within 6 months between two randomized groups. Return was reported in 24.0 of participants in the postcard-only control arm and 34.4 in the arm receiving the postcard plus the family physician reminder letter. The registry reports a positive risk difference of 0.104, a relative risk of 1.433, an odds ratio of 1.661, and a p-value of <0.001. The reported confidence intervals for the comparison measures exclude their respective null values.

The comparison concerns the addition of a signed family physician letter to the standard reminder postcard among overdue women identified through the British Columbia screening program. It does not estimate the effect of the letter in isolation, because the letter arm also received the postcard. Nor does it compare either reminder strategy with receiving no reminder. The outcome is attendance within the stated timeframe, not a diagnosis or a later health outcome.

Statistical evidence of a difference is not the same as a complete account of practical impact. In general, decisions about how to use a result also depend on context, resources, implementation, and the relevance of the study population and outcome. Those broader considerations are not established by the registry results. The trial record also does not report whether women received or read their assigned mailings, or whether the result varied across participant groups.

The findings should not be extended automatically to populations outside the stated eligibility criteria, other screening programs, or other forms of outreach. Longer-term outcomes, screening results, and any consequences beyond attendance are not reported in the registry record. The posted statistics address the specified randomized comparison and endpoint, with the uncertainty and reporting limitations.

16. Why This Trial Matters Statistically

This trial illustrates a useful distinction between an absolute and a relative treatment-effect summary. The risk difference of 0.104 describes the separation in return probabilities on the probability scale. The relative risk of 1.433 and odds ratio of 1.661 express contrasts as ratios, but each uses a different measure. Considering these scales together can make the result easier to interpret without treating the figures as interchangeable.

The comparison also has a clearly defined practical context: both groups received a standard reminder postcard, and the experimental contrast was the addition of a letter signed by a family physician. That design framing matters. A result attributed to the randomized comparison concerns the combined reminder strategy in the letter arm versus the postcard-only strategy, not a physician letter compared with no communication.

The endpoint is a behavior measured within a fixed follow-up period. This makes the reported outcome straightforward to describe, while limiting what it can answer: the registry results address return for screening mammography within 6 months, not what happened after attendance. Clear endpoint boundaries help prevent a statistical difference in attendance from being mistaken for evidence about unreported clinical outcomes.

Finally, the registry shows why estimates and uncertainty should be considered together. A point estimate alone does not indicate how precisely the effect is estimated, while a p-value alone does not express its magnitude. The posted confidence intervals add information about uncertainty, though the record does not provide the methods needed to fully assess their construction. The absent analysis details, missing-data procedures, and original design assumptions remain important limits on statistical evaluation.

17. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry provides limited detail about the study’s statistical methods. It does not report the test used for the primary comparison, the method for constructing confidence intervals, any covariate adjustment, or the prespecified statistical analysis plan. Consequently, the posted estimates can be described, but their analytic implementation cannot be fully reviewed from this record.

The record also does not report missing-outcome counts, follow-up completeness, exclusions, or the analysis population. These omissions make it difficult to assess whether the reported percentages include all randomized participants or how any unavailable outcomes were handled. Baseline characteristics and protocol deviations are not reported either, so the registry alone cannot show how the study groups compared on measured characteristics or whether assignment and follow-up proceeded as intended.

Although the study is listed as double-blinded, the registry does not explain who was masked or how blinding was maintained. Since the interventions were different mailed materials, the practical details of masking and delivery would help readers understand implementation; those details are not reported in the registry record. Receipt, reading, and adherence to the mailed reminders are also not reported.

The trial’s own sample-size justification, assumptions, and any interim analyses are not reported. The available planning illustrations are based on the observed effect and do not substitute for the trial’s original design information. The record lists one outcome measure and no secondary outcomes, limiting evaluation of any broader outcome set. Finally, the reported endpoint is attendance within 6 months; longer-term attendance, screening findings, and other subsequent outcomes are not reported in the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Randomized Trial of Letters From Family Physicians to Encourage Screening Mammography in Overdue Women — NCT02660788.
• Registry record last updated 2021-09-30; status last verified 2021-09.
• Results first posted 2021-09-02.
• 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.

21. Record Summary

NCT02660788 is a completed randomized, double-blinded, parallel-group study sponsored by the British Columbia Cancer Agency. The registry records enrollment of 5498, a start date of 2013-02, and primary completion in 2013-12. The study population was women aged 51-73 years who were overdue for mammography by 6-24 months in the British Columbia screening program.

The comparison was the standard reminder postcard alone versus the postcard plus a family physician-signed reminder letter. The primary outcome was return for screening mammography within 6 months of randomization. The posted percentages were 24.0 in the control arm and 34.4 in the letter arm. The registry reports a risk difference of 0.104, a relative risk of 1.433, an odds ratio of 1.661, and a p-value of <0.001.

The registry does not report secondary outcomes, a detailed statistical plan, missing-data handling, or the original sample-size justification. Interpretation is therefore limited to the posted comparison and endpoint, with the unreported methods and follow-up details remaining unresolved.