Effect of a Patient-Centered Decision App on TOLAC: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of a Patient-Centered Decision App on TOLAC (NCT02646423), a randomized na study. The primary outcome is Number of Participants Who Underwent a Trial of Labor After Cesarean (TOLAC) Delivery.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group trial of a behavioral intervention, titled “Effect of a Patient-Centered Decision App on TOLAC.” The two groups were Prior CD Decision App (PCDDA) and Usual Care - No App. The trial enrolled 1485 participants. The registry lists the University of California, San Francisco as sponsor, gives a start of 2016-01 and primary completion of 2019-06, and records the status as completed.

Participants assigned to the app group were offered access to a tablet and could view the app at their own pace. The description also states that a research assistant would print a summary of the participant’s predicted likelihood of vaginal delivery if she underwent TOLAC. Participants in the comparator group continued usual care without the app. Details about the masking procedure, including who was masked, are not reported in the registry record. Neither the exact randomization procedure nor the allocation concealment approach is reported in the registry record.

The primary measure was the number of participants who underwent TOLAC delivery, recorded in the medical record, during 0-8 weeks after delivery. The posted arm counts were 315 of 727 in the app group and 338 of 732 in usual care. The record notes that primary-outcome data were unavailable for participants who delivered at an outside institution when neither a chart nor an outside questionnaire was obtained: N=8 in the app group and N=3 in usual care. The registry also lists secondary outcomes covering VBAC, knowledge, decisional conflict, decision processes, satisfaction, and maternal morbidity. The original sample-size justification, detailed statistical analysis plan, and any interim-analysis plan 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Prior CD Decision App (PCDDA): no data available for N=8 participants who delivered at outside institution and no chart or outside questionnaire obtained. Usual Care - No App: no data available for N=3 participants who delivered at outside institution and no chart or outside questionnaire obtained.

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 Participants Who Underwent a Trial of Labor After Cesarean (TOLAC) Delivery, measured over 0-8 weeks after delivery.

The primary endpoint is the count of participants who underwent a trial of labor after cesarean delivery, as noted in the medical record. Its timeframe is 0-8 weeks after delivery. The posted results give 315 participants in the Prior CD Decision App group and 338 in the Usual Care - No App group, with arm counts of 727 and 732, respectively.

This endpoint captures whether a participant undertook TOLAC. It is distinct from the secondary VBAC endpoint, which records whether a vaginal birth after cesarean occurred. Someone can undertake a trial of labor without the trial ending in vaginal birth, so the two measures address related but different events. The primary outcome therefore focuses on the delivery approach actually undertaken, while VBAC reflects the delivery outcome.

Recording the event in the medical record provides the stated ascertainment source. The record does not describe how records were reviewed, whether outcome assessors were masked, or how disagreements or incomplete documentation were handled. It also does not explain why TOLAC was selected as the primary endpoint. In general, a primary endpoint gives the main comparison a prespecified focus; the rationale and the protocol’s formal endpoint definition are not reported in the registry record beyond the count and medical-record description.

7. Results Posted in the Registry

• Prior CD Decision App (PCDDA): 43.3% (315/727) versus 46.2% (338/732) on control; risk difference -2.8 percentage points (95% CI -7.9 to 2.3), risk ratio 0.94 (0.84–1.05); unadjusted two-proportion z-test p = 0.274.

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 Underwent Vaginal Birth After Cesarean (VBAC)

• 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:
  • Prior CD Decision App (PCDDA): 31.8% (231/727) versus 31.8% (233/732) on control; risk difference -0.1 percentage points (95% CI -4.8 to 4.7), risk ratio 1.00 (0.86–1.16); unadjusted two-proportion z-test p = 0.982.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prior CD Decision App (PCDDA) and the control. The interval gives the range of effects that remain compatible with the data.

Knowledge About TOLAC and ERCD

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Prior CD Decision App (PCDDA): mean 5.00 versus 5.00 on control; difference 0.00 (95% CI -0.19 to 0.19), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prior CD Decision App (PCDDA) and the control. The interval gives the range of effects that remain compatible with the data.

Decisional Conflict

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Prior CD Decision App (PCDDA): mean 17.20 versus 17.50 on control; difference -0.30 (95% CI -1.73 to 1.13), standardized effect d = -0.02; z-test p = 0.681.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prior CD Decision App (PCDDA) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend beyond the primary question of whether participants underwent TOLAC. They include whether VBAC occurred, knowledge about TOLAC and elective repeat cesarean delivery, decisional conflict, shared decision making, decision self-efficacy, decision satisfaction, and maternal major and minor morbidity. These measures address delivery outcomes as well as participants’ knowledge, decision experience, and maternal outcomes.

The quantitative secondary results posted in detail do not establish a clear broad pattern of differences between groups. Their estimates and uncertainty should be read outcome by outcome; the different measures are not interchangeable, and a result on knowledge or decisional conflict does not answer the primary question about TOLAC uptake. Conversely, a TOLAC result does not establish an effect on VBAC or on the other secondary domains.

Secondary analyses generally carry less confirmatory weight when many outcomes are examined, particularly when the registry does not report whether multiplicity was addressed. Repeated testing can make isolated findings appear noteworthy by chance. The registry lists 12 secondary outcome measures, but a multiplicity strategy and the full analysis plan are not reported in the registry record. The posted secondary outcomes can therefore help describe the range of questions studied, but should not be treated as independent confirmation of the primary result.

Some secondary outcomes have different measurement scales and available group counts. For example, binary event counts and continuous scores require different summaries and interpretations. The number of participants contributing information may also differ across outcomes. A careful reading distinguishes each outcome’s population, timeframe, scale, and uncertainty rather than combining them into a single overall claim about the app.

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

• Number of Participants Who Underwent Vaginal Birth After Cesarean (VBAC)
• Knowledge About TOLAC and ERCD
• Decisional Conflict
• Shared Decision Making
• Decision Self-Efficacy
• Decision Satisfaction
• Maternal Major Morbidity
• Maternal Minor Morbidity

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is between randomized groups: Prior CD Decision App and Usual Care - No App. For a binary endpoint such as whether TOLAC occurred, a risk ratio compares the event proportion in one group with the event proportion in the reference group. A risk ratio of 1 represents equal proportions; a value below 1 indicates a lower proportion in the app group, and a value above 1 indicates a higher proportion. The registry reports a risk ratio of 0.94 for the primary outcome.

What does the confidence interval express?

A confidence interval describes the range of effect estimates reasonably compatible with the data under the statistical model and its assumptions. It also conveys precision: a narrower interval gives a more concentrated range, while a wider interval indicates greater uncertainty. The primary 95% confidence interval is 0.84 to 1.05. Because it crosses 1, the data do not clearly distinguish the observed estimate from no relative difference. A confidence interval is not a guarantee that the true effect lies within its limits, and it does not show the probability that a particular effect is true.

How should the recalculation be understood?

The recalculated risk comparison uses the posted event counts and arm counts to produce a simple, unadjusted comparison. It is not an adjusted model and does not account for covariates or other design features. The recalculated p-value is 0.274. A p-value measures how unusual data at least as incompatible with the null would be if the null hypothesis and model assumptions held; it is not the probability that the null is true. A larger p-value does not demonstrate equivalence, nor does it measure the size or clinical importance of an effect.

For binary outcomes, a risk difference expresses the difference between event proportions in absolute terms, while a risk ratio expresses their relative comparison. The posted recalculation includes a risk-difference estimate and interval, but those values are not needed to interpret the registry’s reported risk ratio. General statistical interpretation should keep the effect scale in view: relative and absolute measures answer different questions and can feel different in practical terms even when based on the same group data.

Why can the secondary outcomes be less conclusive?

The registry lists many outcomes beyond the primary endpoint. When several hypotheses are examined, the chance of at least one apparently unusual finding can increase if each is assessed without accounting for the collection of tests. Whether and how this issue was addressed is not reported in the registry record. The results for secondary measures can still be informative, but they should not be given the same confirmatory weight as the designated primary comparison without a stated analysis plan.

Continuous outcomes such as knowledge and decisional conflict are reported as means with standard deviations. A mean difference compares average scores between groups, while the standard deviation describes variation among participants within a group. In general, the standard deviation is not the uncertainty interval for the mean difference; the latter depends on the group sizes and variability and is expressed by a confidence interval. The registry’s reported analyses use net mean differences for the displayed continuous outcomes.

All these interpretations rely on the data and analysis details recorded in the registry. The statistical method used for the sponsor’s analyses, adjustment choices, handling of missing outcomes, and analysis population definitions are not reported in the registry record. Consequently, the posted numbers support description and cautious comparison, but do not reveal every modeling or data-management decision behind the original analysis.

11. Confidence Intervals and Precision

The primary reported risk ratio is 0.94, and its 95% confidence interval extends from 0.84 to 1.05. That interval crosses 1, the null value for a risk ratio. It therefore includes values compatible with a lower TOLAC proportion in the app group, no relative difference, and a higher proportion. This breadth is important: the point estimate alone cannot convey the range of effects still compatible with the posted data.

The interval is not evidence that all values within its limits are equally plausible, and it does not assign a probability to the effect being beneficial or harmful. It reflects uncertainty under the analysis and assumptions used. The registry does not report the method used for the sponsor’s confidence interval, so the interpretation should remain tied to the posted result rather than to an assumed model.

The recalculated unadjusted analysis also gives an interval that crosses the null, consistent with the sponsor-reported interval at the posted precision. The unadjusted p-value is 0.274. Neither the interval nor the p-value shows that the intervention and comparator are equivalent. Establishing equivalence or noninferiority would require an appropriate design and prespecified margin, which are not reported in the registry record.

Precision also depends on how much outcome information is available. The record notes unavailable primary data for N=8 app-group participants and N=3 usual-care participants who delivered at outside institutions without a chart or outside questionnaire. The consequences of missing outcomes depend on their values and on how missingness was handled; those methods are not reported. Thus, the displayed interval summarizes the posted comparison, while the record leaves some uncertainty about missing-data handling and the scope of the analysis population.

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 displays are planning illustrations based on the observed effect, not the trial’s original design calculations. For the outcomes in these displays, the values are participants per arm, rather than a total across both arms or a total number of events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. Time-to-event displays, if present, use total events; the outcomes discussed in these displays are not time-to-event outcomes.

The 80% power column gives the illustrative number of participants per arm needed for an analysis to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real and the assumptions hold. The 90% column applies the same idea at a higher target chance of detection, which generally requires more participants per arm. These are planning quantities, not observed trial findings.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the required sample size. A smaller effect is harder to distinguish from random variation, so planning to detect a smaller effect requires more participants. When the observed effect is close to zero, the resulting illustrations can become extremely large; they should not be read as a claim that such a future trial is necessary or feasible. They are sensitive to the observed estimate and its uncertainty.

The registry’s original sample-size justification and design assumptions are not reported in the registry record. These calculations are therefore not evidence about the trial’s planning adequacy or its ability to detect a meaningful effect. 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 = 0.462; treatment proportion p₁ = 0.433; average p̄ = 0.448.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7032 = 1.3782.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7029 = 0.5916.
4. n = (1.3782 + 0.5916)² / (-0.0285)² = 4,790.2, rounded up to 4,791 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 <- 0.461748633879781                          # control proportion
p1 <- 0.433287482806052                          # 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(2646423)
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 = 4,791 (80% power), 6,413 (90% power)
 75% of observed effect: n per arm = 8,530 (80% power), 11,418 (90% power)
 50% of observed effect: n per arm = 19,219 (80% power), 25,728 (90% power)
power.prop.test: 4790.2 
Simulated power at n = 4,791 per arm: 0.803 (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-reported primary analysis gives a risk ratio of 0.94 with a 95% confidence interval from 0.84 to 1.05. The simple recalculation from the posted summary counts is consistent with that result at the displayed precision: it also places the estimate near the null and gives an interval that crosses the null. The registry does not flag a discrepancy between the posted analysis and the recalculation.

The sponsor’s analysis is the primary record of the trial’s reported inferential result. The recalculation is an unadjusted check based on summary counts and does not reproduce any undocumented adjustment or analysis choices. The statistical method used for the sponsor’s analysis is not reported in the registry record, so exact methodological equivalence between the two analyses cannot be assumed.

The registry does not provide a sponsor-reported p-value for this comparison. The recalculated unadjusted p-value is 0.274, and it should be identified as a recalculation rather than attributed to the sponsor. Both presentations support a cautious interpretation of the primary estimate, but the sponsor-reported analysis takes precedence as the trial’s own reported result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes. It does not report a multiplicity plan, such as a hierarchy of secondary tests or an adjustment to account for testing several outcomes. Without that information, individual secondary findings should be regarded as exploratory rather than as a set of confirmatory claims. The primary endpoint remains the central comparison, while secondary outcomes provide additional context.

Missing primary-outcome information is explicitly noted for participants who delivered at an outside institution and for whom neither a chart nor an outside questionnaire was obtained: N=8 in the Prior CD Decision App group and N=3 in Usual Care - No App. The posted primary counts are 315 of 727 and 338 of 732, respectively. The registry does not state how unavailable outcomes were handled in the analysis, whether any imputation was used, or whether sensitivity analyses examined alternative assumptions about missing outcomes.

Analysis populations are also not defined in enough detail to determine whether the reported comparison follows an intention-to-treat approach, a per-protocol approach, or another rule. The primary outcome description identifies medical-record ascertainment, but does not report the full participant flow or the analysis-set criteria. Across secondary measures, the posted group sizes vary, and the reasons for each variation are not fully stated in the registry record.

These omissions matter because missing outcomes and selective availability can affect the interpretation of a group comparison, especially if outcome availability is related to group assignment or the outcome itself. They do not show that bias occurred; they mean its possibility cannot be assessed from the registry entries alone. The original statistical plan, missing-data assumptions, and any interim analyses are not reported in the registry record.

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 5% reporting threshold.

The posted adverse-event figures report zero serious adverse events, zero other adverse events, and zero deaths in each group. The at-risk counts are 727 for the app group and 732 for usual care. These entries describe what the registry records for the listed safety categories; they do not by themselves establish that no adverse events occurred outside the recorded definitions or ascertainment process.

The record does not provide serious-event terms, and it does not describe how adverse events were collected, classified, or followed. It also does not report a comparison designed to assess safety differences. A zero count in the posted fields should therefore be read as a registry report, not as proof that the intervention has no risks or that the groups have identical safety profiles. Interpretation is limited by the information available about ascertainment and reporting.

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

The primary posted result is a comparison of recorded TOLAC delivery between participants assigned to the decision app and participants assigned to usual care. The risk-ratio estimate is 0.94, with a 95% confidence interval from 0.84 to 1.05. The interval crosses the no-relative-difference value, and the unadjusted recalculation gives p = 0.274. In this trial record, the data do not provide clear statistical evidence of a difference in the primary endpoint.

This is not proof that the app and usual care produce identical outcomes. The confidence interval permits effects in either direction, and a failure to show a clear difference is not the same as evidence of equivalence. The registry does not report an equivalence or noninferiority design, nor does it give a margin that would define a practically negligible difference.

The result also does not answer every question about decision support. TOLAC is not the same endpoint as VBAC, and neither alone captures knowledge, decisional conflict, shared decision making, self-efficacy, satisfaction, or maternal morbidity. Those outcomes require their own results and interpretation. The primary estimate should not be generalized beyond the trial population and the information recorded in this registry.

Finally, the statistical result does not determine what delivery option is appropriate for any individual. The registry comparison is evidence about groups in a trial, not personal medical guidance. Important design and analysis details—including the original sample-size rationale, missing-data methods, and multiplicity strategy—are not reported in the registry record, which limits how fully the result can be assessed.

18. Why This Trial Matters Statistically

This trial poses a useful statistical question because a decision-support intervention may be intended to influence a choice, while the primary outcome records a concrete delivery approach. Separating TOLAC from VBAC is essential: one measures undertaking labor after cesarean, while the other measures vaginal birth after cesarean. Treating them as the same event would blur a decision process with its eventual outcome.

The randomized comparison also illustrates why a point estimate needs its uncertainty interval. The reported risk ratio of 0.94 is close to the null at the displayed precision, but the 95% confidence interval from 0.84 to 1.05 includes both lower and higher relative event rates. The estimate alone could invite an overly definite reading; the interval makes the uncertainty visible. The unadjusted p-value of 0.274 likewise cannot be interpreted as proof of no effect.

Another statistical lesson is that a trial can ask multiple related questions without those questions having equal evidential status. The primary outcome provides the central test, while secondary measures examine other aspects of delivery and decision experience. Without a reported multiplicity plan, secondary findings need particular caution. Missing primary data and varying group sizes across outcomes also make transparent population definitions and sensitivity analyses important, yet those details are not reported in the registry record.

Finally, planning illustrations based on the observed effect are not substitutes for the original trial design rationale. They show how target effect size and desired power affect planning requirements under stated assumptions, but they cannot recover the investigators’ original reasoning. Together, these points make the record a practical example of interpreting effect estimates, precision, endpoint distinctions, and reporting gaps in a randomized clinical trial.

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.

Several trial-specific details needed for a complete assessment are not reported in the registry record. The eligibility criteria and recruitment procedures are not described in detail, so the population to which the findings may apply cannot be characterized fully from this record. The record identifies single masking but does not say who was masked or how masking was maintained.

The app description indicates tablet access and a printed summary of predicted likelihood of vaginal delivery, but the app’s full content, delivery fidelity, participant use, and any accompanying counseling are not reported. The comparator is described as usual care, without a fuller account of what care entailed or whether it varied across participants.

For the primary outcome, the record identifies medical-record review and notes unavailable data for outside deliveries without a chart or outside questionnaire. It does not explain the missing-data analysis, provide a full account of outcome ascertainment, or report sensitivity analyses. The analysis population and the method used for the sponsor’s statistical comparison are also not stated. This limits assessment of whether the posted result reflects all randomized participants under a defined analysis rule.

The registry does not report the original sample-size justification, a detailed statistical analysis plan, multiplicity handling, or an interim-analysis plan. The number and breadth of secondary outcomes make the absence of a reported multiplicity approach particularly relevant when interpreting those outcomes. These reporting gaps do not establish that the trial was conducted improperly; they constrain what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of a Patient-Centered Decision App on TOLAC — NCT02646423.
• Registry record last updated 2021-02-02; status last verified 2021-01.
• Results first posted 2021-02-02.
• 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.

23. Record Summary

The registry record describes a completed randomized, single-masked, parallel-group trial sponsored by the University of California, San Francisco. It enrolled 1485 participants and compared the Prior CD Decision App with usual care without the app. The primary endpoint was the number of participants who underwent TOLAC delivery, recorded in the medical record during 0-8 weeks after delivery.

The posted primary result was a risk ratio of 0.94, with a 95% confidence interval from 0.84 to 1.05. The interval crosses the null value, so the result does not establish a clear difference between groups. Primary-outcome data were unavailable for N=8 app-group participants and N=3 usual-care participants under the circumstances described in the record. Secondary outcomes addressed VBAC and several decision-related and maternal measures. Details of the original design rationale, analysis plan, multiplicity handling, and missing-data methods are not reported in the registry record.