Impact of Family History and Decision Support on High-risk Cancer Screening: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Impact of Family History and Decision Support on High-risk Cancer Screening (NCT02247336), a randomized na study. The primary outcome is Number of Patients With Provider Referral for Risk-appropriate Colorectal Cancer Screening.

2. Clinical Question

The clinical question is whether asking patients to enter family health history into the MeTree platform at enrollment, with tailored screening recommendations, is associated with more provider referrals for colorectal cancer screening appropriate to the patient’s risk level than delaying platform use until 12 months following enrollment. The registry describes the rationale as a lack of a standardized system for collecting and updating family health history, assessing risk, and communicating screening recommendations.

The question concerns the referral process, rather than only whether screening was completed. The registry also reports recommended colorectal cancer screening as a secondary outcome, so referral and screening uptake represent related but distinct steps. The primary comparison is between assigned trial groups; the registry does not report enough detail to establish whether every patient assigned to immediate platform use completed the assessment or received the recommendations.

3. Trial Design

The registry describes a randomized, unmasked, parallel-group trial and lists the condition as colorectal cancer. Enrollment was 505. The trial status is completed; the recorded start date is 2017-08-01, and the primary completion date is 2020-07-13. The registry lists phase as NA. The intervention is behavioral: use of the MeTree family health history platform.

In the Immediate group, patients were to complete the platform at enrollment. In the Delayed group, patients were to complete it 12 months following enrollment. This timing defines the contrast of interest: platform access and tailored recommendations during the period before the primary outcome assessment versus delayed access. The registry does not report whether other aspects of care were held constant between groups, or whether providers received additional study procedures beyond the referral information described in the record.

The primary outcome was assessed at 12 months. Its analysis population is described as patients who completed the family health history assessment, since the risk level was necessary to determine whether a referral was risk-appropriate. The reported primary outcome denominators are 252 for Immediate and 253 for Delayed. Those are the denominators used for that posted outcome, not a statement about completion or availability of every other outcome.

There are two posted secondary outcomes: receipt of recommended colorectal cancer screening and referral for genetic consultation. Their analysis denominators differ from the primary outcome denominators. The registry record does not report detailed eligibility criteria, participant demographics, recruitment locations, the method used to generate the random allocation sequence, allocation concealment, or the trial’s original sample-size justification. Those details should not be inferred from the randomized label or the recorded enrollment.

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: The analysis sample is the number of patients who completed the family health history assessment, as risk level was necessary to determine risk-appropriate referrals.

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 Number of Patients With Provider Referral for Risk-appropriate Colorectal Cancer Screening, measured over 12 months.

The primary endpoint counts patients who received a provider referral for colorectal cancer screening that was consistent with the risk stratum determined by the family health history platform. It is recorded as a participant count at 12 months. A referral is the event being assessed; the endpoint is not simply whether the platform was completed, whether a recommendation was generated, or whether a patient ultimately underwent screening.

This measure is relevant to the trial question because family history can inform risk assessment, and the platform was designed to produce recommendations tailored to that history. Comparing the count of patients with an appropriate referral between the Immediate and Delayed groups therefore evaluates whether the intervention period coincided with differences in the referral process. The registry’s stated analysis sample includes patients who completed the family history assessment, because the risk stratum was needed to judge referral appropriateness.

The posted counts are 219 of 252 in Immediate and 232 of 253 in Delayed. These counts describe the analyzed outcome groups; they do not by themselves explain why a participant did or did not receive a referral. The registry record does not report the underlying risk-stratum distribution, the referral criteria by stratum, or whether referrals were independently adjudicated. Nor does the endpoint establish that a referral led to screening. Screening receipt is separately listed as a secondary outcome.

7. Results Posted in the Registry

• Delayed: 91.7% (232/253) versus 86.9% (219/252) on control; risk difference 4.8 percentage points (95% CI -0.6 to 10.2), risk ratio 1.06 (0.99–1.12); unadjusted two-proportion z-test p = 0.081.

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 of Participants Who Received Recommended Colorectal Cancer Screening

• 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:
  • Delayed: 62.4% (68/109) versus 53.4% (55/103) on control; risk difference 9.0 percentage points (95% CI -4.3 to 22.2), risk ratio 1.17 (0.93–1.47); unadjusted two-proportion z-test p = 0.185.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Who Received Referral for Genetic Consultation

• 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:
  • Delayed: 6.7% (1/15) versus 4.5% (1/22) on control; risk difference 2.1 percentage points (95% CI -13.2 to 17.5), risk ratio 1.47 (0.10–21.67); unadjusted two-proportion z-test p = 0.779.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delayed and the control. The interval gives the range of effects that remain compatible with the data.

The two secondary outcomes examine other parts of the screening pathway: receipt of recommended colorectal cancer screening and referral for genetic consultation. Taken together, their unadjusted point estimates have the same directional pattern as the primary risk-difference estimate, with the Delayed group’s estimated event proportion higher. Their uncertainty differs, reflecting the amount of outcome information available for each comparison.

These outcomes complement rather than replace the primary endpoint. A provider referral, a completed screening procedure, and a referral for genetic consultation are different events. Findings for one cannot be assumed to establish the same effect on another. In particular, the registry does not describe whether the primary referral outcome led to screening, and the separate secondary measures do not establish a causal pathway between the outcomes.

The genetic consultation outcome is based on very sparse event counts, which limits precision and makes relative estimates unstable. The screening outcome has more event information, but its unadjusted comparison also has uncertainty. The posted secondary findings should therefore be read as supportive descriptive evidence about related processes, not as independent confirmation of the primary result.

Unadjusted secondary results carry less weight for several reasons. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary outcomes. When several outcomes are examined, the chance of at least one apparently notable result can increase, even if each comparison is considered separately. Without a reported plan for controlling that issue, isolated secondary p-values should not be treated as definitive. These outcomes are most useful for describing the broader pattern and identifying questions for further evaluation, while keeping the primary outcome and the sponsor’s reported analysis distinct.

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

• Number of Participants Who Received Recommended Colorectal Cancer Screening
• Number of Patients Who Received Referral for Genetic Consultation

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each patient either received a risk-appropriate colorectal cancer screening referral or did not, as represented in the posted count. For a binary outcome, the observed risk is the proportion of participants with the event in a group. The registry gives the event counts and denominators, and the unadjusted recalculation compares those group risks without covariate adjustment.

What does the risk difference describe?

The risk difference is the risk in Delayed minus the risk in Immediate. Its estimate is 0.048, with a 95% confidence interval from -0.006 to 0.102. A positive risk difference indicates a higher observed event proportion in Delayed; a negative value would indicate a higher proportion in Immediate. The interval includes zero, the value corresponding to no difference in risks. This scale is directly interpretable as an absolute difference in event proportions, although the result is still subject to sampling uncertainty and the limits of the analysis population.

How do relative measures differ?

The recalculation also gives a risk ratio and an odds ratio. A risk ratio compares the risks in the groups as a ratio, whereas an odds ratio compares the odds of the event. These relative measures use different scales and should not be read as absolute percentage-point differences. When an outcome is common, an odds ratio and a risk ratio can differ materially in magnitude. The primary comparison’s recalculated risk ratio is 1.055, with a confidence interval from 0.993 to 1.121; the recalculated odds ratio is 1.665, with a confidence interval from 0.934 to 2.966. Both intervals include the value representing no relative association on their respective scales.

What does the p-value add?

The unadjusted p-value is 0.081. In general, a p-value describes how unusual data at least as discordant with a specified null model would be if that model were true and the calculation’s assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the probability that a finding is due to chance. A p-value also does not convey the size or clinical importance of an effect. The risk difference and confidence interval provide complementary information about the estimated magnitude and uncertainty.

Why is logistic regression reported?

The sponsor’s reported primary analysis is labeled logistic regression and gives an odds ratio, a 95% confidence interval, and a p-value. Logistic regression is a method commonly used for binary outcomes; it models the odds of an event. Depending on the model specification, it can estimate an unadjusted association or account for covariates. The registry record does not report the covariates, model specification, reference coding, or other details needed to determine the precise interpretation of that analysis. The sponsor’s result is therefore best described using the reported method and values, without assuming which characteristics were included.

The recalculated results are simple unadjusted comparisons from the posted group counts. They are not a reproduction of a regression model. A difference between a regression estimate and an unadjusted calculation can arise from differences in modeling, adjustment, group coding, or analytic populations, but the registry record does not establish which explanation applies in this trial. The reported sponsor analysis and the unadjusted recalculation should therefore be kept distinct rather than treated as interchangeable estimates.

Why can rare outcomes be unstable?

For a binary outcome with few events, the estimate can be highly sensitive to the observed event pattern. The genetic consultation outcome has very sparse counts, and its relative-effect confidence intervals are wide. In general, sparse data make estimates less stable and can produce substantial uncertainty, particularly for ratios. This is a statistical limitation, not evidence that the outcome is unimportant. The confidence interval and the event count both matter when interpreting such results.

All these methods depend on what was recorded and on the analysis population. The registry identifies completion of family health history assessment as necessary for the primary risk-appropriate referral analysis. It does not provide the full missing-data procedure, the randomization implementation details, or the sponsor model specification. Those absences limit how far the numerical results can be interpreted beyond the comparisons explicitly reported.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.048, and its 95% confidence interval extends from -0.006 to 0.102. The interval includes zero, so the summary data do not rule out no difference in the unadjusted risk comparison. At the same time, the upper end allows for a positive difference, and the lower end allows for a small difference in the opposite direction. The interval is therefore a more informative account of uncertainty than the point estimate alone.

A confidence interval is a range produced by a statistical procedure that, under its assumptions, would cover the underlying parameter at the stated rate across repeated applications. It is not a range that assigns a probability to the fixed true effect after seeing these data. Its width reflects the precision of the estimate: a wider interval leaves more uncertainty about the magnitude and direction of the effect.

The recalculated relative-effect intervals also include their no-association values: the risk ratio is 1.055 with a confidence interval from 0.993 to 1.121, and the odds ratio is 1.665 with a confidence interval from 0.934 to 2.966. The odds-ratio interval is especially broad, illustrating that the relative estimate is not precise. Each effect measure answers a different question, so the numerical values should not be compared as if they were on the same scale.

Precision is also affected by the analysis denominator and the outcome frequency. The primary endpoint has many recorded referral events in both groups, but its interval still spans zero. The secondary genetic consultation outcome has sparse events and correspondingly substantial uncertainty. The registry does not report additional information about missing observations or the calculation of the sponsor model’s standard errors, so those aspects cannot be assessed from the record.

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 and not total events. They illustrate the group size that a new study would require under the stated planning assumptions if it aimed to detect a specified fraction of the observed effect. The primary outcome is a participant-count endpoint, so the figures are participants per arm.

The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The planning figures are calculated from the observed effect and are not the trial’s original design assumptions; the original sample-size justification is not reported in the registry record.

The 80% power column describes the planned chance of detecting the assumed effect under the specified model and assumptions if that effect were the true effect. The 90% power column uses a higher target chance of detection under those same planning conditions. These are design-planning concepts, not guarantees that a future study will detect an effect, and they do not determine whether an observed result is important.

Rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the required per-arm size changes with the assumed effect. Smaller effects require more participants per arm to achieve the same target power, because they are harder to distinguish from random variation. The displayed figures are planning illustrations, not observed power for this completed trial.

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 = 0.869; treatment proportion p₁ = 0.917; average p̄ = 0.893.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4371 = 0.8567.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4358 = 0.3668.
4. n = (0.8567 + 0.3668)² / (0.0479)² = 651.1, rounded up to 652 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 <- 0.869047619047619                          # control proportion
p1 <- 0.91699604743083                          # 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(2247336)
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 = 652 (80% power), 872 (90% power)
 75% of observed effect: n per arm = 1,216 (80% power), 1,627 (90% power)
 50% of observed effect: n per arm = 2,862 (80% power), 3,831 (90% power)
power.prop.test: 651.1 
Simulated power at n = 652 per arm: 0.809 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as logistic regression, with an odds ratio of 0.7, a 95% confidence interval from 0.4 to 1.2, and p = 0.16. The posted group order is Immediate and Delayed, but the registry record does not report the model’s reference coding or covariates. The direction of the reported odds ratio should therefore not be translated into a group-specific effect without those details.

The unadjusted recalculation from the posted primary counts gives a risk difference of 0.048 for Delayed relative to Immediate, with a 95% confidence interval from -0.006 to 0.102 and p = 0.081. This calculation uses a different effect scale and is not a reconstruction of the sponsor’s logistic regression. The registry record does not report enough model detail to explain any difference between the estimates or p-values.

The sponsor analysis and the recalculation both indicate uncertainty rather than a clearly resolved group difference: the reported sponsor interval includes the odds-ratio value corresponding to no association, and the unadjusted risk-difference interval includes zero. Because the discrepancy flag is false, the posted analyses can be described together without a discrepancy warning. The sponsor’s reported model result remains the trial’s own analysis, while the recalculation is a supplementary unadjusted comparison based on posted summary counts.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and two secondary outcomes. It also records two analyses. The record does not report whether the outcomes were ordered in a testing hierarchy, whether an adjustment for multiple comparisons was planned, or whether the secondary outcomes were intended to support formal confirmatory claims. In general, examining several outcomes can increase the chance of a nominally unusual result. Without a reported multiplicity strategy, secondary p-values should be interpreted cautiously and in context rather than as stand-alone evidence.

The record does not report how missing outcome data were handled, whether participants with incomplete assessments were excluded, or whether imputation was used. The primary population is described as patients who completed the family health history assessment because risk level was required to evaluate referral appropriateness. The primary outcome denominators are 252 for Immediate and 253 for Delayed, while the secondary denominators vary by outcome. This indicates that the posted analyses do not all use the same denominators, but the record does not explain the reasons for those differences.

The registry record does not report an intention-to-treat analysis, a per-protocol definition, or a sensitivity analysis for missing data. It also does not report the allocation concealment process, interim analyses, or the original statistical analysis plan. These details matter because they help readers assess whether the analysis followed the randomized assignment, how incomplete observations affected estimates, and whether the outcome analysis was specified before results were known. Their absence from the registry record does not establish that such procedures were not used; it means their use cannot be evaluated from the posted information.

For the sponsor’s logistic regression, the model specification and covariates are not reported. The registry also does not report how the sponsor addressed multiple outcomes or whether the reported model was prespecified. These limitations do not invalidate the posted estimates, but they restrict assessment of the analysis choices and the strength of any confirmatory interpretation.

16. 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 adverse-event figures report zero serious adverse events in Immediate and zero in Delayed. The record also reports zero other adverse events in each group. Deaths are recorded as 2 in Immediate and 0 in Delayed. These are descriptive counts in the registry record; they do not establish the cause of death or whether an event was related to the platform or trial participation.

The adverse-event denominators are 252 for Immediate and 253 for Delayed. The registry lists no top serious adverse-event terms. It does not report further details about event definitions, timing, severity beyond the serious-event classification, attribution, or completeness of safety surveillance. A zero count in the posted categories means no events were recorded in those categories in the registry results; it should not be expanded into a claim that no other health events occurred.

Because this was a behavioral platform intervention, the event counts should be read as the safety information recorded for the study rather than as evidence about a medical treatment’s effects. The registry figures alone do not establish comparative safety or explain the deaths reported for Immediate.

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

The registry results address whether immediate versus delayed use of a family health history platform was associated with differences in referrals appropriate to colorectal cancer risk at 12 months. The primary unadjusted estimate is a positive risk difference for Delayed relative to Immediate, but its confidence interval includes zero. The sponsor’s logistic regression result also has a confidence interval that includes the no-association value. Together, these results are uncertain; they do not establish a clear difference in the primary referral outcome.

Uncertainty is not the same as evidence of equivalence. The confidence interval leaves room for effects in either direction and for a positive difference. Establishing that two strategies are sufficiently similar would require an equivalence or non-inferiority framework with an appropriate margin and analysis; the registry record does not report such a framework. Nor does a non-small p-value prove that the groups had identical outcomes.

The primary outcome concerns a provider referral judged appropriate to family-history risk. It does not establish whether screening was completed, whether a genetic consultation occurred, or whether colorectal cancer outcomes changed. Those are distinct questions, and the registry’s secondary outcomes provide separate, uncertain information about screening receipt and genetic consultation referral.

The results also apply to the participants and analysis populations represented in the registry record. The primary analysis is described as requiring completion of the family history assessment. Missing-data handling and details of the participant population are not reported in the registry record, so the findings should not be generalized beyond the study context without considering those limitations.

In practical statistical terms, the posted evidence is best characterized by the estimated effect and its uncertainty, not by a binary label of success or failure. The results document what was observed in this trial’s reported analyses, while leaving uncertainty about the magnitude and direction of any underlying difference.

18. Why This Trial Matters Statistically

This trial raises a statistical question that is broader than comparing screening recommendations alone: a family-history tool is intended to connect risk assessment with provider action and, ultimately, patient screening. Each step is a distinct outcome. Separating those steps helps prevent a referral result from being mistaken for evidence that screening was completed or that health outcomes changed.

The randomized, parallel-group design creates a structured comparison of immediate and delayed platform use. At the same time, the primary endpoint depends on completing a family health history assessment so that risk-appropriate referral can be judged. That makes the analysis population an important part of interpretation: the reported primary comparison is not simply a count across everyone enrolled, but a count in the population described as having completed the assessment.

The trial also illustrates why an effect estimate and its precision should be read together. The primary point estimate is positive for Delayed in the unadjusted comparison, yet the confidence interval includes zero. A directional point estimate alone cannot settle the question, and an interval spanning no difference does not prove equivalence. Reporting both supports a more measured interpretation than relying on a single p-value.

Finally, the secondary outcomes and safety counts add context while also demonstrating the limits of registry summaries. Some outcome information is sparse, analysis denominators differ, and details about missing data, multiplicity, and the sponsor’s model are not reported in the registry record. Those features matter for assessing strength of evidence and for planning further research, without changing what the posted results actually record.

19. 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 report detailed eligibility criteria, participant characteristics, or recruitment setting. Without those details, it is difficult to judge how closely the analyzed patients represent other populations who might use a family health history platform. The record also does not describe the process for generating and concealing random allocation, so implementation of the randomized design cannot be assessed from the posted information.

The primary outcome requires a completed family health history assessment to determine risk-appropriate referral. The record does not report how many patients were unable to complete the assessment, why the primary analysis population differs from enrollment, or how incomplete outcomes were handled. Since the primary endpoint depends on risk classification, missing assessment information may affect which patients contribute to the analysis; the size and direction of any effect cannot be determined from the registry record.

The registry does not report referral criteria by risk stratum, the method for verifying referrals, or whether outcome assessors were blinded. The trial is listed as unmasked, and the platform intervention itself could not be described as masked in the record. The available information does not establish whether awareness of group assignment influenced referral documentation or outcome ascertainment.

The sponsor’s logistic regression model details are not reported, including covariates and group coding. The registry also does not report an adjustment for multiple outcomes, a prespecified hierarchy, or the original sample-size justification. The secondary genetic consultation result is based on sparse events, limiting precision. Finally, outcomes are reported at 12 months; longer-term screening behavior and clinical outcomes are not included in the posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Impact of Family History and Decision Support on High-risk Cancer Screening — NCT02247336.
• Registry record last updated 2023-07-27; status last verified 2023-07.
• Results first posted 2021-08-19.
• 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.

23. Record Summary

NCT02247336 is a completed randomized, unmasked, parallel-group trial of the MeTree family health history platform for colorectal cancer risk assessment and screening. Enrollment was 505. The Immediate group was to complete the platform at enrollment, while the Delayed group was to complete it 12 months following enrollment.

The primary outcome counted patients receiving a provider referral for colorectal cancer screening consistent with the risk stratum determined by the platform, assessed at 12 months. The unadjusted recalculation shows a positive risk difference for Delayed relative to Immediate, with a confidence interval that includes zero. The sponsor’s reported logistic regression result also has a confidence interval that includes the no-association value.

Secondary outcomes cover recommended screening receipt and referral for genetic consultation. The registry record does not report detailed missing-data procedures, multiplicity handling, or full model specifications. The posted estimates therefore describe the recorded outcomes while leaving important aspects of analysis and precision uncertain.