Safety and Efficacy Study of IPG Patient With Home Monitoring: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of IPG Patient With Home Monitoring (NCT01523704), a randomized na study. The primary outcome is Evaluation for Equivalence of the Number of Patients Who Meet the Composite Safety Endpoint Between Home Monitoring Group(HM) and Control Group Which is HM + Conventional In-office Follow-up.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group study with no masking and a planned comparison between Home Monitoring follow-up and Home Monitoring plus conventional in-office follow-up. The study is listed as completed. Its stated purpose was to assess whether Home Monitoring could reduce office follow-up visits without compromising patient safety. The condition listed is bradyarrhythmia, and the devices under study are BIOTRONIK systems.

The Home Monitoring group had fewer scheduled in-office interrogations than the Control group. Both groups had in-office visits at the 3-month and 27-month follow-ups; the Control group also had visits at the 9-month, 15-month, and 21-month follow-ups. The Home Monitoring group’s device status at those intervening follow-ups was evaluated through Home Monitoring. These scheduled procedures describe the intended follow-up contrast, but the registry record does not report adherence to the schedule or how unscheduled visits were handled.

The registry lists enrollment of 1327, while the numbers contributing to posted results differ across outcomes. For example, the primary endpoint lists 558 participants in the Home Monitoring group and 550 in the Control group, and the secondary outcomes have their own reported group sizes. The registry record does not explain these differences or report the analysis populations used for each outcome. The original sample-size justification, randomization details, allocation concealment, and trial-specific statistical analysis plan are not reported in the registry record. The trial is marked as completed, but the posted completion status does not by itself establish that all randomized participants contributed to every analysis.

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: 1327 patients were enrolled. At the 3-month follow-up, 53 patients were excluded (24 withdrew consent, 17 death, 8 lost to follow-up and 4 protocol deviation). 1274 patients 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.

6. Primary Endpoint

The registry lists the primary outcome as Evaluation for Equivalence of the Number of Patients Who Meet the Composite Safety Endpoint Between Home Monitoring Group(HM) and Control Group Which is HM + Conventional In-office Follow-up, measured over 2 years.

The primary endpoint counts participants meeting a composite safety endpoint over 2 years. The registry defines the safety event rate using death, stroke, and cardiovascular-related serious adverse events requiring surgical interventions, with examples including device explants or lead revision. A composite endpoint combines several clinically important event types into one outcome. This can make a safety comparison more informative when the individual types of event are not frequent enough to support a precise separate comparison, while also requiring care because the components may differ in severity and frequency.

The registry frames the comparison as an equivalence or non-inferiority question and states that 5% was set as the allowable clinically significant difference. Its description says that rejecting the null hypothesis would indicate that the safety event rate in the Home Monitoring group is equivalent, or non-inferior, to that in the Control group. However, the hypothesis text is malformed and refers inconsistently to 24-month and 12-month durations. The precise formal hypothesis and analysis procedure are therefore not fully clear from the registry record.

The posted primary results count 61 participants with the endpoint in the Home Monitoring group and 65 in the Control group. The registry record does not report the component-specific primary endpoint counts by treatment group or explain how participants with more than one component event were counted.

7. Results Posted in the Registry

• Home Monitoring Group: 10.9% (61/558) versus 11.8% (65/550) on control; risk difference -0.9 percentage points (95% CI -4.6 to 2.9), risk ratio 0.93 (0.67–1.29); unadjusted two-proportion z-test p = 0.642.

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.

The Median (IQR) Numbers of In-office Follow-up（FU) Visits Per Patient-year

• 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:
  • Home Monitoring(HM): mean 0.69 versus 2.00 on control; difference -1.31 (95% CI -1.36 to -1.26), standardized effect d = -3.16; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Home Monitoring(HM) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Efficacy of Home Monitoring：Average Cost for In-office Follow-up Per Patient-year

• 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:
  • Home Monitoring Group: mean 21,065 versus 23,552 on control; difference -2,487 (95% CI -5,076 to 101.51), standardized effect d = -0.11; z-test p = 0.060.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Home Monitoring Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes describe two practical aspects of follow-up: the frequency of in-office visits and their average cost per patient-year. In the posted results, the Home Monitoring group has a lower reported mean for both measures. The statistical certainty differs: the visit comparison has a confidence interval entirely below zero, while the cost comparison’s interval includes zero. This pattern suggests that the posted evidence is clearer for the measured visit frequency than for the average cost difference. Cost is not a direct substitute for visit frequency, since the registry does not report all cost components or how costs were measured.

These secondary results complement, but do not determine, the primary safety comparison. A reduction in in-office visits is relevant to the stated rationale for the study, while the primary endpoint addresses the safety concern accompanying a change in follow-up strategy. Evidence about one outcome cannot settle the other. The primary comparison remains uncertain, and the registry’s equivalence framing requires a formal assessment against its stated margin rather than reliance on a non-significant conventional test.

The registry reports unadjusted secondary comparisons and does not describe a multiplicity strategy. When multiple outcomes are examined, unadjusted tests can overstate the strength of evidence if interpreted as separate confirmatory tests. The secondary endpoints also have their own analysis sizes and measurement properties, which the registry does not fully explain. Accordingly, their results are useful for understanding the direction and precision of the posted observations, but they should carry less weight than a prespecified primary analysis and should not be treated as independent proof of a broad benefit across outcomes.

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

• The Median (IQR) Numbers of In-office Follow-up（FU) Visits Per Patient-year
• Efficacy of Home Monitoring：Average Cost for In-office Follow-up Per Patient-year

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute? Random allocation is intended to make treatment groups comparable, on average, with respect to both measured and unmeasured characteristics at the point of assignment. This helps support a causal interpretation of differences between groups, provided allocation was implemented as intended and participants are analysed appropriately. The registry identifies the study as randomized, but the sequence-generation method, concealment procedures, and details of the analysis population are not reported in the registry record. Randomization does not eliminate the need to account for missing data, non-adherence, or differences in who contributes to each outcome.

Why is the primary outcome binary? The primary endpoint is a count of participants who meet the composite safety definition. For this kind of outcome, each participant is classified as having or not having the endpoint during the stated follow-up period. The reported risk difference compares the event proportions in the two groups by subtracting the Control proportion from the Home Monitoring proportion. A negative estimate means the observed proportion was lower in Home Monitoring; it does not, on its own, show that the strategies are equivalent or that a clinically important difference has been excluded.

How should the confidence interval and p-value be read? A confidence interval gives a range of effect estimates compatible with the data under the statistical method used, while reflecting sampling uncertainty. A narrower interval indicates greater precision than a wider interval on the same scale. The p-value assesses how unusual the data would be under a specified null hypothesis; it is not the probability that the null hypothesis is true, and it does not measure clinical importance. For an equivalence or non-inferiority question, the key issue is whether the uncertainty interval is sufficiently contained within the prespecified margin under the intended analysis. A p-value for a conventional test of no difference does not answer that question by itself.

How do the secondary outcomes differ? Office follow-up visits and follow-up costs are reported as means with standard deviations, and their comparisons are expressed as mean differences. A mean difference summarizes the difference between group averages. The standard deviation describes variation among observations within a group; it is not the uncertainty around the estimated mean difference. The reported confidence intervals for the mean differences describe uncertainty in the comparisons. The office-visit outcome is labelled as a median in its title, but the registry lists the parameter as a mean and reports means with standard deviations. This inconsistency should be kept in mind when interpreting the statistic.

Costs are often highly variable, with some observations substantially different from the rest. In general, skewness and extreme values can make a mean sensitive to a small number of observations; the registry record does not report the cost distribution, any transformation, or a method designed for skewed costs. The cost comparison should therefore be understood from the posted mean, standard deviation, and confidence interval, without assuming that the data were normally distributed.

What do the posted analyses establish? The registry reports unadjusted comparisons for the primary and secondary outcomes, but the reported-analyses lists for the secondary outcomes are empty, and the sponsor’s analysis details are not reported in the registry record. The two-year follow-up period is stated for the outcomes, but the record does not report a time-to-event analysis, a handling method for participants lost to follow-up, or whether the primary outcome was assessed by intention to treat, per protocol, or another analysis population. Those choices can matter, especially in equivalence and non-inferiority studies, where departures from assigned treatment can influence the estimated difference.

General statistical context: adjustment for baseline covariates can sometimes improve precision or address chance imbalance, but the registry does not report whether such adjustment was used. Likewise, a prespecified analysis plan can help distinguish planned comparisons from exploratory ones; the trial-specific plan is not reported in the registry record. The posted results should be interpreted as the comparisons available in the registry rather than as a complete account of the sponsor’s statistical analysis.

Why can over-dispersion matter? General statistical context: over-dispersion occurs when observed variability exceeds what a chosen statistical model expects. If a model underestimates variability, standard errors and confidence intervals can be too optimistic. The registry reports means and standard deviations for the secondary outcomes, but does not report a model-based analysis or an assessment of over-dispersion. It is therefore not possible to determine from the record whether that issue was relevant to the analyses.

Why should multiple outcomes be treated cautiously? Each separate test creates an opportunity to observe a result that looks notable by chance. Testing several outcomes without adjustment or a stated hierarchy can increase the risk of false-positive interpretations. The registry does not report a multiplicity adjustment or a hierarchy covering the secondary outcomes. Their unadjusted p-values are therefore best regarded as descriptive evidence, not as a complete confirmatory testing strategy.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.009, with a 95% confidence interval from -0.046 to 0.029. The interval includes zero, so the posted data are compatible with a range of possible group differences, including differences favouring either follow-up strategy. Its breadth indicates that the primary estimate is not highly precise enough to pin down a single narrow effect range. The interval should be considered alongside the registry’s stated 5% margin, but the record’s malformed hypothesis description and lack of a reported sponsor analysis limit a definitive equivalence interpretation.

The office-visit mean difference has a confidence interval from -1.359 to -1.261. This interval is comparatively narrow and lies below zero, so the direction of the observed difference is estimated more precisely than the primary risk difference’s direction relative to zero. The cost mean difference has a confidence interval from -5076 to 101.5, which includes zero. Its range allows both a lower mean cost in Home Monitoring and a small higher mean cost, so the cost comparison is less conclusive about direction.

Confidence intervals quantify uncertainty under the analysis used; they do not account automatically for bias, missing data, outcome misclassification, or differences between the planned and actual analysis. The registry does not report enough detail to assess those sources of uncertainty. Precision also differs by endpoint and cannot be inferred from enrollment alone: the numbers included in the posted analyses vary across outcomes, and the underlying variability differs between measures.

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 estimates are illustrations based on the observed effect, not a report of how the original trial was designed. They assume 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. These estimates are participants per arm for the outcomes expressed as participant counts or continuous measurements; the general convention for time-to-event planning estimates would be total events, but no time-to-event outcome is listed among these results.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the chosen effect under its assumptions. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. Neither column describes the probability that the completed study found a true effect, nor does it measure the probability that a result is correct. This is not observed power.

The rows use the full observed effect and smaller fractions of that effect. Smaller effects are harder to distinguish from random variation, so the planning estimates require more participants per arm as the effect used becomes smaller. The estimates are especially sensitive to the observed effect: an effect observed in one study can be unstable and may not represent the effect in a future study. The original trial’s own sample-size assumptions and justification are not reported in the registry record. The planning figures should therefore be read as conditional illustrations, not as a reconstruction of the trial’s protocol or a claim about whether the completed enrollment was adequate.

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 = 0.118; treatment proportion p₁ = 0.109; average p̄ = 0.114.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4490 = 0.8801.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4490 = 0.3779.
4. n = (0.8801 + 0.3779)² / (-0.0089)² = 20,145.5, rounded up to 20,146 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 <- 0.118181818181818                          # control proportion
p1 <- 0.109318996415771                          # 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(1523704)
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 = 20,146 (80% power), 26,969 (90% power)
 75% of observed effect: n per arm = 36,119 (80% power), 48,353 (90% power)
 50% of observed effect: n per arm = 81,950 (80% power), 109,707 (90% power)
power.prop.test: 20145.5 
Simulated power at n = 20,146 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary safety endpoint and two secondary outcomes, but does not report a statistical analysis plan describing an outcome hierarchy, multiplicity adjustment, or rules for selecting analyses. The posted comparisons are unadjusted. Without a stated approach to multiple testing, secondary p-values should be interpreted cautiously: the more outcomes and analyses considered, the greater the possibility that some findings appear notable by chance. The record does not state whether other planned outcomes or subgroup analyses were omitted from the posted results.

Missing-data handling is not reported in the registry record. The number of participants contributing to an outcome can differ from the number randomized, and the posted group sizes vary across the primary and secondary outcomes. The record does not say whether those differences reflect missing measurements, eligibility for a particular analysis, withdrawals, or another reason. It also does not report imputation, sensitivity analyses, or methods for participants with incomplete follow-up. This matters because estimates can be biased if outcome availability differs between groups or is related to participants’ health or follow-up experience.

The analysis populations are not specified. The registry does not report whether the primary comparison used all randomized participants, participants who adhered to their assigned follow-up strategy, or another population. This is particularly important for an equivalence or non-inferiority question, where the choice of population and handling of crossovers can affect the result. The record also does not report how protocol deviations, withdrawal, or unscheduled follow-up were handled.

The formal analysis plan, including any prespecified equivalence procedure and the treatment of the stated 5% margin, is not reported in the registry record. As a result, the posted unadjusted estimates can be described, but the registry does not provide enough information to verify whether they correspond to the trial’s full planned analysis.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: the number of the composite primary endpoint (11.8%), death (8.2%), the number of cardiovascular surgery (3.6%), the number of stroke (1.4%).

The primary results list 61 participants with the composite endpoint in the Home Monitoring group and 65 in the Control group. A separate adverse-event listing reports 68 participants with a serious adverse event in each group, as well as 46 deaths in Home Monitoring and 41 in Control. It also lists other adverse events for 7 participants in Home Monitoring and 16 in Control. These listings are not interchangeable: the registry does not explain whether the adverse-event categories use the same definitions, follow-up, or analysis populations as the primary endpoint. In particular, it does not reconcile the separate serious-event counts with the primary endpoint counts.

The serious-event terms list the composite primary endpoint as 11.8%, death as 8.2%, cardiovascular surgery as 3.6%, and stroke as 1.4%. These are descriptive figures, not a comparative analysis of each component. The registry does not report confidence intervals or group-specific comparisons for those terms. The figures should therefore be read as safety listings, not as proof that one follow-up strategy has more or fewer serious events.

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

The posted results describe a randomized comparison of two follow-up strategies in which both groups used Home Monitoring, but the Control group had additional scheduled in-office interrogations. The primary endpoint estimate is close to zero on the risk-difference scale, and its confidence interval includes zero. This means the posted primary comparison does not establish a conventional difference between strategies. It also does not, by itself, establish equivalence or non-inferiority. Those conclusions require the formal margin-based analysis and interpretation, which are not fully documented in the registry record.

The secondary results suggest that the observed frequency of in-office visits was lower in the Home Monitoring group, with a relatively narrow interval for the mean difference. The cost estimate also favours a lower average in Home Monitoring, but its interval includes zero, so the direction of the cost difference is less certain. These results address different practical questions and should not be combined into a single claim about overall effectiveness or resource use.

The findings do not show that every participant received the assigned monitoring schedule, nor do they establish how missing data or deviations affected the results. The record does not describe individual event timing, component-specific primary endpoint comparisons, or the full analysis population. It also does not provide enough detail to judge whether the posted analyses match the original statistical plan.

Accordingly, the results support a cautious description of the observed group estimates and their precision. They should not be treated as medical advice, as proof of safety equivalence, or as a guarantee that the observed differences would recur in other settings. The registry’s stated purpose and posted outcomes are informative, but important aspects of the formal analysis remain unreported.

17. Why This Trial Matters Statistically

This trial raises a statistically important question about how to evaluate a change in follow-up practice when safety is intended to be preserved. A conventional test for a difference and an equivalence or non-inferiority assessment answer different questions. Failure to find a statistically significant difference does not show that two strategies are sufficiently similar. A defensible equivalence conclusion depends on a clinically justified margin, a clear prespecified method, and a confidence interval interpreted against that margin. The registry states a 5% margin but does not provide a sufficiently clear hypothesis description or report the sponsor’s formal analysis.

The study also illustrates why outcomes tied to service use and safety need separate interpretation. The posted visit-frequency comparison is relatively precise, whereas the cost comparison is less conclusive, and the primary safety interval remains broad enough to allow effects in either direction. One endpoint cannot stand in for another: fewer visits do not establish safety equivalence, and an uncertain cost estimate does not erase the observed visit-frequency pattern.

Finally, the differences in reported analysis sizes and the lack of detail about missing data, analysis populations, multiplicity, and the original sample-size plan limit how far the results can be generalized. These are not minor reporting details for an equivalence-oriented study; they affect how confidently the observed estimates can be linked to the intended question. The registry record is useful for understanding the trial’s design and posted results, while leaving material uncertainty about the full inferential analysis.

18. Limitations

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

Several limitations specific to this record affect interpretation. The primary hypothesis description is malformed and mixes 24-month and 12-month durations, even though the primary outcome timeframe is listed as 2 years. The record states a 5% allowable clinically significant difference but does not report the formal sponsor analysis or explain how that margin was applied. This makes it difficult to verify the intended equivalence or non-inferiority conclusion from the posted comparison alone.

The primary endpoint results and adverse-event listing contain different serious-event counts: the primary outcome lists 61 and 65 participants, while the adverse-event listing reports 68 in each group. The registry does not reconcile these figures or clarify whether definitions, analysis populations, and observation periods match. Component-specific primary endpoint counts by group are also not reported. Such differences may reflect distinct outcome definitions or populations, but the record does not establish the reason.

Outcome-specific analysis sizes vary, and the record does not explain why. It does not report missing-data methods, analysis populations, adherence, crossovers, or protocol deviations. The office-visit outcome title refers to a median and IQR, but its parameter and posted summaries identify a mean and standard deviation. The registry does not clarify this inconsistency. Cost methods and the range of costs included are not described.

Finally, the trial-specific statistical analysis plan, original sample-size assumptions, multiplicity strategy, and detailed randomization procedures are not reported in the registry record. These omissions limit assessment of prespecification, robustness, and the relation between posted estimates and the planned analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of IPG Patient With Home Monitoring — NCT01523704.
• Registry record last updated 2021-01-27; status last verified 2021-01.
• Results first posted 2021-01-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized, open-label, parallel-group study comparing Home Monitoring follow-up with Home Monitoring plus conventional in-office follow-up among patients with bradyarrhythmia and an implantable pulse generator. The primary outcome was the number of participants meeting a composite safety endpoint over 2 years. The posted risk difference was -0.009, with a 95% confidence interval from -0.046 to 0.029 and an unadjusted p-value of 0.642.

The secondary results report fewer mean in-office visits in the Home Monitoring group, while the estimated mean cost difference is less conclusive. Important details of the formal equivalence analysis, missing-data handling, analysis populations, and multiplicity strategy are not reported in the registry record. The results are best interpreted as posted group estimates with their stated uncertainty, rather than as a complete account of the trial’s statistical analysis.