Baroreflex Activation Therapy for Heart Failure: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Baroreflex Activation Therapy for Heart Failure (NCT02627196), a randomized na study. The primary outcome is Rate of Cardiovascular Mortality and Heart Failure Morbidity.

2. Clinical Question

The comparison is between two treatment strategies for the selected heart-failure population, not a comparison of the device with no care. Both groups were to receive guideline-directed medical therapy. The intervention added device implantation, while the comparator received medical management alone. The registry describes a randomized, parallel-group trial without masking. These features define the intended comparison, but the posted outcome does not by itself establish whether any difference was caused by the device or whether the same result would apply to people outside the registry’s eligibility description.

The registry’s stated primary objective was to assess whether the device strategy reduced the event rate relative to medical management. The posted rate estimates are close: 0.46 events per patient-year for device and medical management, and 0.48 for medical management. The reported analysis does not establish a statistically significant superiority result. That finding describes the uncertainty in the comparison; it is not proof that the strategies are equivalent or that an important difference is impossible.

3. Trial Design

NCT02627196 is a completed, randomized, parallel-group trial sponsored by CVRx, Inc. The registry lists an enrollment of 1090 and describes the trial as having no masking. The two intervention groups were device and medical management, and medical management alone. The intended study population was people with heart failure meeting the clinical criteria described in the registry summary, excluding people eligible for or actively receiving cardiac resynchronization therapy.

In the device group, participants were to receive an implanted BAROSTIM NEO System alongside optimal, stable guideline-directed medical therapy. In the comparator group, participants were to receive optimal, stable guideline-directed medical therapy without the device. Medication choices were determined by the participant’s physician. The registry does not describe one identical drug regimen for everyone, so the contrast is between the assigned strategies rather than between fixed medication packages.

The registry gives a start date of 2016-04-19 and primary completion in 2023-10, and lists the status as completed. It anticipated a total trial duration of approximately 5 years, while noting that an individual participant’s enrollment duration would depend on when they entered the trial. For the primary endpoint, the timeframe is from randomization until the data-cut date used for endpoint analysis; median follow-up was 3.6 years per patient.

The posted primary endpoint outcome reports 159 participants in the device-and-medical-management group and 160 in the medical-management group. Those are the counts attached to the posted endpoint rates, rather than the registry’s overall enrollment figure. The registry record does not explain the relationship between those counts and the overall enrollment, so no reason for the difference can be inferred from the posted information. The allocation ratio and details of sequence generation or concealment are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: The protocol indicates a subject is considered enrolled upon signing the informed consent form. A total of 1090 subjects provided informed consent and were enrolled. Following completion of screening procedures and application of eligibility criteria per protocol, 467 subjects met randomization criteria and were assigned to study arms. The remaining enrolled subjects were considered screen failures and did not proceed to randomization.

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 Rate of Cardiovascular Mortality and Heart Failure Morbidity, measured over From randomization until data-cut date for the endpoint analysis. Median follow-up was 3.6 years per patient..

The primary endpoint is the rate of cardiovascular mortality or worsening heart failure that leads to hospitalization, cardiac assist device, or heart transplant. It is expressed as events per patient-year, rather than simply as the proportion of participants who experienced an event. The registry reports that the event rate was calculated using a negative binomial model to account for varying follow-up times. Median follow-up was 3.6 years per patient.

A rate-based endpoint is useful when participants contribute different amounts of observed time. A participant followed for a shorter period contributes less exposure time than someone observed longer; an event rate relates the event count to time under observation. This allows a comparison that accounts for variable follow-up, although its interpretation still depends on how events and exposure time are defined and analyzed.

The endpoint combines cardiovascular mortality with specified worsening-heart-failure events. It therefore reflects more than one type of outcome. The registry’s description does not provide further detail about endpoint adjudication, how recurrent events were handled, or whether the components were also analyzed separately in the primary analysis. Those details are not reported in the registry record.

The posted rates were 0.46 events per patient-year for device and medical management and 0.48 for medical management. These are estimates, not exact underlying event frequencies, and their confidence intervals express uncertainty. The endpoint is intended to evaluate the event burden over follow-up; it does not alone describe all possible benefits, harms, quality-of-life effects, or experiences associated with either strategy.

7. Results Posted in the Registry

• Medical Management: 0.48 versus 0.46 (Rate of Events Per Patient-Year) on control; rate ratio 1.04 (95% CI 0.62–1.75, derived from the posted confidence limits); p ≈ 0.872.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a rate, not a simple risk measured at one fixed time. A rate uses event occurrence in relation to accumulated observation time. When follow-up differs across participants, the amount of time each participant contributes also differs. The registry says negative binomial regression was used to account for varying follow-up times. The purpose of a rate model is to compare event occurrence while taking exposure time into account, rather than treating every participant as if observed for the same duration.

Why use a negative binomial model?

In a basic count model, a common simplifying assumption is that event counts vary around their mean in a particular way. Clinical event counts can be more variable than that assumption allows, a situation called over-dispersion. A negative binomial model can accommodate this extra variability. In general, allowing for over-dispersion can produce uncertainty estimates that better reflect variability in event counts. The registry identifies the model but does not report diagnostic checks, model specification details, or whether any covariates were included.

The outcome is reported as events per patient-year with 95% confidence intervals. An event rate summarizes events relative to follow-up exposure. The confidence interval describes statistical uncertainty around an estimated rate under the analysis model; it is not a range containing a fixed percentage of individual participants’ outcomes. The group intervals are 0.32 to 0.65 for device and medical management and 0.33 to 0.7 for medical management. These intervals concern each group’s rate, not directly the difference between groups.

What does the between-group estimate represent?

The sponsor-reported analysis is a negative binomial regression analysis labeled as a risk ratio. Its estimate is 0.94, with a 95% confidence interval from 0.57 to 1.57 and p = 0.82. A ratio of one represents no relative difference in the measure being compared. The reported interval includes that value, and the p-value does not provide evidence of superiority under the conventional interpretation of the reported test. The registry does not report the model’s covariates, standard-error method, or other implementation details.

The separate recalculation uses the posted summary rates to form an unadjusted rate ratio, with medical management compared relative to device and medical management. Its estimate is 1.043 and its reported p-value is 0.872. It is not the same analysis as the sponsor’s regression result. It does not adjust for participant-level information or use details unavailable in the posted summaries. The record indicates no discrepancy, but the sponsor’s analysis remains the reported analysis of the trial.

How should a p-value be read?

A p-value describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Here, the reported p-value is 0.82, while the recalculated p-value is 0.872. Neither is evidence of a statistically significant superiority result. A non-significant result does not prove no effect; the estimate and its uncertainty must be considered together.

Confidence intervals and p-values address related but distinct aspects of inference. The interval conveys a range of values compatible with the data and model at the stated confidence level, while the p-value summarizes evidence against a null value under the test. For the reported ratio, the confidence interval spans values on both sides of the no-difference value. This is consistent with uncertainty about both the direction and magnitude of the relative effect.

What is not specified?

The registry record does not report enough detail to reconstruct the complete analysis. The exact handling of recurrent events, endpoint adjudication, covariate adjustment, missing outcome data, censoring, or deviations from assigned treatment is not reported in the registry record. The registry also does not provide the original statistical analysis plan or explain whether analyses were prespecified in the form reported. The description states that rates were calculated with negative binomial regression to account for varying follow-up, but further implementation choices should not be inferred.

General statistical interpretation also depends on design and conduct. Randomization is intended to support a fair comparison of assigned strategies, while lack of masking can matter when outcomes or their ascertainment involve judgment. The registry identifies the trial as randomized and unmasked, but does not give enough information to assess sequence concealment, adherence, crossover, or blinding of endpoint assessment. Those are limitations of what can be concluded from the registry record, not evidence that any particular problem occurred.

10. Confidence Intervals and Precision

The confidence intervals communicate how precisely the event rates and relative effect were estimated. For device and medical management, the posted rate is 0.46 events per patient-year, with a 95% confidence interval from 0.32 to 0.65. For medical management, the rate is 0.48, with a 95% confidence interval from 0.33 to 0.7. The estimates are close, but the intervals allow a range of plausible underlying rates and overlap substantially.

The sponsor-reported relative estimate is 0.94, and its 95% confidence interval runs from 0.57 to 1.57. This interval includes the no-relative-difference value and permits effects in either direction. Its width signals that the reported estimate is not precise enough to rule out a range of potentially important relative effects. The p-value of 0.82 is consistent with the interval’s failure to exclude the no-difference value.

Precision is not the same as clinical importance. A confidence interval does not determine whether any effect within its range would matter to patients, and the registry does not state a threshold for a clinically important difference. It also does not establish that every value in the interval is equally plausible. The interval is interpreted under the analysis and its assumptions.

The unadjusted re-calculation gives an estimate of 1.043 and p = 0.872; its interval is reported with more decimal places than the output rules allow, so its limits are not restated. The sponsor’s interval remains the registry’s reported analysis. Taken together, the posted estimates do not precisely distinguish the strategies, and a non-significant result should not be read as proof of equivalence.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the original trial’s design calculations. For this rate endpoint, the figures are participants per arm, not total events. They are calculated using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The registry’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned participants per arm under the stated assumptions for a design with an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column gives the corresponding per-arm planning figure for a design with a 90% chance under the same assumptions. These are design probabilities conditional on the assumed effect and model; they are not probabilities that the treatment is effective.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller-effect rows require more participants per arm: detecting a smaller difference is harder because it is less distinguishable from random variation. For example, planning for 75% of the observed effect requires 9,158 participants per arm for 80% power and 12,260 participants per arm for 90% power. Planning for 50% of the observed effect requires 20,714 and 27,730 participants per arm, respectively. At 100% of the observed effect, the corresponding figures are 5,125 and 6,861.

These are planning illustrations, not observed power. They do not tell whether the completed trial had adequate power for its original question, because the original assumptions are not reported. They also do not establish that the observed effect is the effect future studies should target. The figures depend on the stated assumptions, including equal allocation and the normal approximation, and should be read as conditional design calculations rather than as additional trial outcomes.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.4600; treatment rate λ₁ = 0.4800 events per patient-year; follow-up T = 3.60 years.
2. n = (1.96 + 0.842)² × (1/0.4600 + 1/0.4800) / (3.60 × [ln(1.043)]²) = 5,124.3, rounded up to 5,125 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
lambda0 <- 0.46                      # control rate, events per patient-year
lambda1 <- 0.48                      # treatment rate
tt      <- 3.6                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2627196)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 5,125 (80% power), 6,861 (90% power)
 75% of observed effect: n per arm = 9,158 (80% power), 12,260 (90% power)
 50% of observed effect: n per arm = 20,714 (80% power), 27,730 (90% power)
Simulated power, Poisson counts, n = 5,125 per arm: 0.804
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.629

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

13. Analyses Reported by the Sponsor

The sponsor-reported primary analysis is the negative binomial regression result: risk ratio 0.94, 95% confidence interval 0.57 to 1.57, and p = 0.82. This is the trial’s posted analysis and should be distinguished from the simple recalculation using the displayed group rates.

The recalculation gives a rate ratio of 1.043 for medical management relative to device and medical management, with p = 0.872. It is unadjusted and based on summary statistics. Its comparison is oriented in the opposite direction from the sponsor’s reported ratio, and the registry labels the sponsor’s measure as a risk ratio. The two estimates therefore should not be treated as identical quantities or as interchangeable analyses.

The registry indicates no discrepancy between the sponsor’s result and the recalculation. The recalculation is useful as a transparent check on the posted rates, but it cannot reproduce participant-level regression or any analysis details not included in the record. The sponsor’s regression analysis is the relevant reported result for the trial’s primary endpoint. Neither result demonstrates statistical superiority, and neither establishes equivalence.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures and five analyses, while the primary outcome is the rate of cardiovascular mortality and heart failure morbidity. The record does not describe whether the five analyses formed a prespecified family of tests, whether an adjustment for multiple comparisons was planned, or how the primary endpoint was prioritized relative to other outcomes. A multiplicity strategy is not reported in the registry record.

Multiplicity matters when several hypotheses are tested. With multiple opportunities to declare a result, the chance of at least one false-positive finding can increase if tests are interpreted without accounting for their number or relationship. Adjustment methods and hierarchical testing can address that concern, but the registry does not report whether either approach was used. The posted primary p-value should therefore be interpreted as reported, without assuming a particular multiplicity correction.

Missing-data procedures are also not reported in the registry record. The endpoint timeframe runs from randomization until the data-cut date for endpoint analysis, and median follow-up was 3.6 years per patient. However, the record does not specify how incomplete follow-up, withdrawal, loss to follow-up, or missing endpoint information was handled. It also does not describe censoring rules or the assumptions used for participants with incomplete observation.

The registry identifies the study as randomized and unmasked. It does not report the analysis population definition, such as whether the primary analysis followed intention-to-treat principles, nor does it describe treatment adherence, crossovers, or exclusions from analysis. The outcome counts attached to the primary rates are 159 for device and medical management and 160 for medical management, but the record does not explain how these relate to overall enrollment. No analysis population or missing-data strategy should be inferred from those counts alone.

The absence of these details limits assessment of the robustness of the reported estimate. It does not show that a particular method was omitted or that missingness biased the result. It means that the registry record does not provide enough information to evaluate those questions independently.

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: heart failure - acute decompensated heart failure (unrelated) (31.3%), death, cardiovascular-related (unrelated) (10.0%), cardiac arrhythmias - ventricular tachycardia/vf (unrelated) (9.4%), other cardiac (unrelated) (8.8%), gastroenterology (unrelated) (7.5%).

The registry lists serious adverse events affecting 121 participants in the device-and-medical-management group, with 163 at risk, and 121 participants in the medical-management group, with 160 at risk. Other adverse events affected 134 participants in the device-and-medical-management group, with 163 at risk, and 128 participants in the medical-management group, with 160 at risk. The registry also lists 33 deaths in the device-and-medical-management group and 42 in the medical-management group.

These are descriptive counts. They do not establish that the device caused or prevented any event, and they should not be interpreted as adjusted comparisons. The record does not explain the relationship between the safety group counts and the endpoint counts, or provide detailed methods for attribution, event collection, or follow-up in the safety summary.

The registry’s leading serious adverse-event terms include acute decompensated heart failure (unrelated), listed as 31.3%; cardiovascular-related death (unrelated), 10.0%; ventricular tachycardia/VF (unrelated), 9.4%; other cardiac (unrelated), 8.8%; gastroenterology (unrelated), 7.5%; and cardiac chest pain (unrelated), 6.7%. These terms are presented as listed in the registry, including the attribution “unrelated.” The record does not specify the denominators for these term percentages in the posted summary, so they should not be read as risks for either treatment group.

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

The posted primary outcome estimates show event rates of 0.46 per patient-year with device and medical management and 0.48 per patient-year with medical management. The sponsor-reported negative binomial regression result has a risk ratio of 0.94, a 95% confidence interval from 0.57 to 1.57, and p = 0.82. This analysis does not demonstrate statistically significant superiority of one strategy on the primary endpoint.

That conclusion is narrower than saying the strategies are the same. The confidence interval includes the no-difference value and remains compatible with relative effects in either direction. The trial result does not prove equivalence, rule out a meaningful difference, or establish that the device has no effect. A non-significant superiority test answers whether the data provide sufficient evidence for superiority under the reported analysis; it does not answer every question about effectiveness or safety.

The endpoint combines cardiovascular mortality and specified worsening-heart-failure events, so the overall estimate does not show the result for each component separately. The rate also does not reveal the proportion of participants who experienced an event or how repeated events were distributed. Those details are not reported in the registry record.

The outcome is specific to the comparison and population described: device implantation added to guideline-directed medical therapy versus medical management alone in the selected heart-failure population. It should not be generalized automatically to people outside those eligibility characteristics, to other treatment regimens, or to a different comparison. The registry’s safety counts provide additional descriptive information but do not establish causal effects or a complete benefit-harm assessment.

In short, the registry reports no statistically significant difference for its primary superiority analysis, but the uncertainty is broad. The result is best read as inconclusive about the range of relative effects compatible with the data, rather than as evidence that the strategies are interchangeable.

17. Why This Trial Matters Statistically

This trial raises a useful statistical challenge: the primary endpoint is an event rate measured over participant time, rather than a single-timepoint outcome. Follow-up can vary, and a rate analysis needs to account for different exposure times. The registry states that negative binomial regression was used for this purpose, making the model choice and its assumptions central to interpreting the result.

The endpoint also combines cardiovascular mortality with worsening-heart-failure events that lead to specified interventions or hospitalization. Composite outcomes can provide a broader measure of event burden, but a combined estimate does not reveal whether the components have similar frequencies or effects. The component-specific primary results are not reported in the registry record.

Another statistical lesson is the distinction between absence of significant evidence and evidence of no effect. The reported confidence interval includes the no-difference value and spans effects in both directions. The p-value is not statistically significant, but the result does not establish equivalence. Precision, model assumptions, and the clinical interpretation of the composite all remain relevant.

The registry also allows readers to contrast a sponsor-reported regression analysis with a simple recalculation from displayed rates. Those approaches can serve different purposes: the latter is a transparent summary-based check, while the reported regression is the trial’s stated analysis. Their estimates should not be treated as identical when their contrast direction and statistical formulation differ.

Finally, the registry’s overall enrollment and the counts attached to the primary outcome are not the same, and the record does not explain why. This highlights why analysis populations, follow-up, missing-data handling, and sample-size assumptions matter for judging how much a trial result can support. Where those details are absent, statistical interpretation should remain bounded by the information actually reported.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record does not provide the original sample-size justification, so the relationship between the planned enrollment and the posted primary endpoint counts cannot be evaluated from the record alone. It lists enrollment of 1090, while the primary rates are reported for 159 participants in the device-and-medical-management group and 160 in the medical-management group. The reason for this difference is not reported in the registry record and should not be inferred.

Important analysis details are also absent, including the full negative binomial model specification, any covariate adjustment, handling of recurrent events, endpoint adjudication procedures, and methods for missing or incomplete follow-up. The registry gives median follow-up of 3.6 years per patient and states that rates account for varying follow-up, but that does not supply all information needed to assess model assumptions or reproduce the analysis.

The trial was unmasked. The registry does not report whether endpoint assessors were masked, how treatment adherence or crossover was handled, or whether the primary analysis followed an intention-to-treat approach. These are unknowns in the registry record, not evidence that the trial had a specific bias.

The primary endpoint is composite, and the registry record does not give separate primary-analysis results for cardiovascular mortality and worsening-heart-failure events. Safety information is descriptive, with no detailed methods for attribution or comparative safety analysis in the posted summary. The registry also does not report a multiplicity plan, missing-data strategy, or original statistical analysis plan. These omissions constrain interpretation of precision, robustness, and the broader benefit-harm picture.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Baroreflex Activation Therapy for Heart Failure — NCT02627196.
• Registry record last updated 2026-03-10; status last verified 2026-02.
• Results first posted 2026-03-10.
• 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

NCT02627196, Baroreflex Activation Therapy for Heart Failure, is a completed randomized, parallel-group trial sponsored by CVRx, Inc. It compared the BAROSTIM NEO System plus guideline-directed medical therapy with medical management alone in a selected heart-failure population. The registry lists enrollment of 1090 and no masking.

The primary endpoint was the rate of cardiovascular mortality or worsening heart failure leading to hospitalization, cardiac assist device, or heart transplant. Rates were calculated using negative binomial regression to account for varying follow-up. The posted rates were 0.46 events per patient-year for device and medical management and 0.48 for medical management. The reported risk ratio was 0.94, with a 95% confidence interval from 0.57 to 1.57 and p = 0.82.

The primary superiority analysis did not demonstrate a statistically significant difference. Its interval remains compatible with effects in either direction, so the result does not establish equivalence or rule out a meaningful difference. Several design and analysis details, including the original sample-size justification and missing-data methods, are not reported in the registry record.