Effects of Low-calorie Sweetened Beverage Restriction in Youth With Type 1 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Low-calorie Sweetened Beverage Restriction in Youth With Type 1 Diabetes (NCT04385888), a randomized na study. The primary outcome is Glycemic Variability.

2. Clinical Question

The registry summary frames the study as an investigation of whether low-calorie sweeteners are helpful or harmful in relation to preventing diabetes complications among children with type 1 diabetes. The posted primary outcome is narrower: it is a comparison of change in time in range over the study period. The record also lists visceral adiposity and change in inflammatory cytokines as secondary outcomes. Results are posted for inflammatory cytokines, while a numerical result for visceral adiposity is not reported in the registry record.

This distinction matters when interpreting the question. A short-term difference in a measured glycemic outcome is not itself a direct test of long-term complications or of every possible effect of low-calorie sweetener consumption. The study description specifies a restriction period of 12 weeks; it does not describe a long-term follow-up result. The clinical question can therefore be read as a focused comparison of the assigned behavior strategies and selected measured outcomes, rather than as a complete assessment of all possible benefits and harms.

3. Trial Design

The registry describes a randomized, single-masked, parallel behavioral study. Random allocation means participants were assigned to one of the study strategies by a random process; parallel design means the groups followed their assigned strategies over the same study period rather than crossing between strategies. The record says the study was single-masked but does not identify who was masked, so the masking procedure cannot be characterized further from the registry record.

The planned intervention was low-calorie sweetener restriction. Participants in that group were instructed to avoid low-calorie sweetened beverages and other sources of low-calorie sweeteners for 12 weeks, using unsweetened alternatives such as plain or sparkling water. The usual-consumption group continued low-calorie sweetener consumption as usual. The registry classifies the intervention as behavioral, not as a drug treatment.

The registry lists enrollment as 62 and the study status as completed. The recorded study start was 2020-10-28, and primary completion was recorded as 2023-12-30. These are study-record dates and do not by themselves describe the duration of every participant’s follow-up. The primary outcome timeframe is baseline versus weeks 11–12, while the posted inflammatory cytokine outcome uses baseline versus week 12.

The primary result is restricted to children who completed the study, according to the registry description. The arm-level primary outcome summaries contain 13 participants in the low-calorie sweetener restriction group and 13 in the usual-consumption group. The registry also lists parent arms, but parent outcome values are not reported for the primary endpoint. The reason for the difference between the overall enrollment and the outcome-specific participant counts is not reported in the registry record, and no participant flow explanation should be inferred from these counts alone.

The original sample-size rationale, masking details, randomization procedure, and the trial’s prespecified statistical analysis plan are not reported in the registry record. The registry’s planning illustrations based on observed effects are separate from the original design assumptions.

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 reason that the number started does not equal the total enrollment is because there was a run-in period, prior to randomization, where 3 children (6 total participants including the child's parent) were lost to follow-up.

Run-in Period

Randomized to Intervention or Control

Analysis population for the primary outcome, as defined in the registry: The outcome was measured only among children who completed the study.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Baseline characteristics were not collected for parents.

6. Primary Endpoint

The registry lists the primary outcome as Glycemic Variability, measured over Baseline vs Weeks 11-12.

The registry labels the primary endpoint “Glycemic Variability” and defines it as change in Time in Range (TIR), with percent as the unit. The comparison is between baseline and weeks 11–12. The reported outcome values are means of a continuous measure, accompanied by standard deviations. The registry says the endpoint was measured only among children who completed the study.

In general, time in range describes the share of measured time that a glucose value falls within a defined target range. It is used as a way to characterize glucose patterns, complementing measures that summarize glucose levels at a single point or over a period. The target range and the measurement procedures are not reported in the registry record, so the precise operational definition of TIR cannot be established from this record.

The endpoint’s label and its description are not identical: “Glycemic Variability” is the title, while the specific outcome is described as change in TIR. These should not be treated as interchangeable measures without further protocol detail. The posted result is about the mean change in TIR, not a direct summary of every aspect of glucose variability.

Using a change from baseline focuses the comparison on how the measured outcome shifted over the intervention period. In general, change outcomes can be useful for evaluating short-term movement in a clinical measure, but their interpretation depends on how baseline and follow-up values were collected and analyzed. Those details, including any adjustment for baseline values, are not reported in the registry record. The posted endpoint should therefore be interpreted as a comparison of reported mean changes among study completers, not as a fully described estimate from a specified adjusted model.

7. Results Posted in the Registry

• Low-calorie Sweetener Restriction: mean 2.00 versus 3.91 on control; difference -1.91 (95% CI -3.90 to 0.08), standardized effect d = -0.74; z-test p = 0.060.

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.

Change in Inflammatory Cytokines (TNF-alpha)

• 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 errors.
• Result:
  • Low-calorie Sweetener Restriction: mean 0.08 versus -0.23 on control; difference 0.31 (95% CI 0.10 to 0.52), standardized effect d = 1.14; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Low-calorie Sweetener Restriction than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists visceral adiposity and change in inflammatory cytokines as secondary outcomes. Numerical results are posted for change in TNF-alpha, while a numerical visceral adiposity result is not reported in the registry record. The available secondary information is therefore incomplete, and an overall pattern across all listed secondary outcomes cannot be evaluated from the record.

TNF-alpha is a biomarker outcome rather than the primary TIR measure. Its posted mean difference and interval are distinct from the primary result and do not provide a direct explanation for the TIR estimate. A difference in a secondary biomarker may help describe the range of outcomes considered, but it cannot establish that the intervention changed the primary outcome or that a biomarker difference translates into a clinical effect.

Secondary results generally carry less confirmatory weight when they are not the principal prespecified question, particularly if many outcomes have been examined. Testing several outcomes creates more opportunities for a nominally unusual result to occur by chance. The registry does not report whether multiplicity was addressed, how outcomes were prioritized in the analysis plan, or whether the secondary analyses were exploratory.

Accordingly, the TNF-alpha result can be described as a posted secondary finding with an unadjusted comparison, but should not be treated as decisive evidence on its own. The lack of a posted visceral adiposity result further limits a broad reading across the secondary outcomes. The record does not provide a joint analysis or a rationale linking the secondary outcomes to a single overall conclusion.

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

• Visceral Adiposity
• Change in Inflammatory Cytokines (TNF-alpha)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons are mean differences for continuous outcomes. For the primary result, the difference is calculated as the mean change in the low-calorie sweetener restriction group minus the mean change in the usual-consumption group. The same direction of subtraction applies to the TNF-alpha comparison. A negative value means the restriction-group mean is lower; a positive value means it is higher. The direction alone does not say whether a change is beneficial or harmful.

What does a mean difference summarize?

A mean difference compares the average observed change in one group with the average observed change in the comparison group. It keeps the outcome in its original unit, which is percent for the primary TIR result and pg/mL for TNF-alpha. This makes the estimate interpretable on the scale of the measurement. It does not show how every participant responded, and it does not describe the full distribution of individual outcomes.

For the primary outcome, the group means are 2.0 and 3.91, and the recalculated difference is -1.91. For TNF-alpha, the group means are 0.08 and -0.23, and the recalculated difference is 0.31. These are simple, unadjusted comparisons from the posted group summaries. They do not account for baseline values, covariates, missing outcomes, or any other features unless those were already incorporated into the reported summary statistics; such analytic details are not reported in the registry record.

What do standard deviations and standard errors describe?

A standard deviation describes the spread of individual observations around a group mean. The primary endpoint reports a standard deviation of 2.59 in each group. A standard error instead describes uncertainty in an estimated mean. The TNF-alpha endpoint reports standard errors of 0.07 and 0.08. These measures have different interpretations and should not be compared as if they were the same quantity.

For the recalculated comparisons, the posted summary statistics are used to form the estimated differences and their intervals. A standard error for a mean difference reflects uncertainty in that estimated contrast. In general, uncertainty depends on both within-group variability and the amount of information contributing to the estimate. The record’s outcome counts are 13 for each reported child group. The registry does not report a model-based analysis that could clarify whether other design features or covariates were incorporated.

How should the confidence intervals be read?

A confidence interval gives a range of values that are compatible with the estimate under the method used to calculate it. In general, an interval’s width conveys precision: a narrower interval indicates less uncertainty under that method, while a wider interval indicates more. The confidence level and complete calculation procedure are not reported in the registry record, so the interval should be read as posted rather than attributed to a particular model or confidence level.

The primary interval extends from -3.901 to 0.081 and includes zero. Zero represents no mean difference between groups on the outcome scale. The interval therefore includes both a negative difference and values close to no difference. The secondary TNF-alpha interval extends from 0.102 to 0.518 and does not include zero. This distinction describes the calculated intervals; it does not by itself address multiplicity, clinical importance, or possible bias.

What does an unadjusted p-value tell the reader?

A p-value measures how surprising data at least as extreme as the observed result would be under a statistical model in which the null hypothesis of no group difference holds. It is not the probability that the null hypothesis is true, nor does it indicate the probability that the result will replicate. The posted p-values are unadjusted: 0.06 for the primary comparison and 0.004 for TNF-alpha. Their interpretation depends on the analysis plan and the number of questions evaluated. The registry does not report a multiplicity adjustment or a detailed inferential plan.

In general, multiple testing can increase the chance that at least one result appears unusual by chance when many outcomes or comparisons are examined. This is why an unadjusted secondary p-value should be considered alongside the endpoint hierarchy, prespecified analysis plan, and related evidence. The registry does not describe those elements sufficiently to reconstruct a confirmatory testing strategy.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model assumes. When it is not accounted for, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. The outcomes in this record are continuous means, and no over-dispersion assessment or model details are reported. This concept is relevant as a general statistical caution, not as a claim that over-dispersion occurred in this study.

The comparisons and interval estimates are recalculated from posted summary statistics rather than drawn from a reported analysis set. The registry lists no reported analyses. The record does not state whether the results were adjusted, whether a particular distributional assumption was checked, or how missing observations were handled. These limitations constrain what can be concluded from summary-level recalculation.

11. Confidence Intervals and Precision

The primary mean difference is -1.91 percentage points, with an interval from -3.901 to 0.081. The estimate is centered on a lower mean change in the restriction group, but the interval reaches slightly above zero. Thus, the posted summary does not precisely distinguish a negative between-group difference from little or no difference. The interval also allows values farther from zero on the negative side, which signals meaningful uncertainty in the estimated contrast.

The group standard deviations are both 2.59, indicating appreciable spread in observed changes relative to the mean difference. A standard deviation describes variation among measurements, whereas the interval describes uncertainty in the estimated contrast; they answer different questions. The record does not report an adjusted model, a confidence level, or additional interval-calculation details. The interval should therefore be understood as the posted recalculated estimate, not as proof of a particular model’s assumptions.

The TNF-alpha difference is 0.31 pg/mL, with an interval from 0.102 to 0.518. Unlike the primary interval, this interval does not include zero. Its narrower separation from zero in the posted result does not make it a replacement for the primary endpoint, and its interpretation is tempered by its secondary status and unadjusted p-value.

Precision is not the same as clinical importance. The registry does not specify a threshold for a clinically meaningful change in TIR or TNF-alpha. It also does not report the original sample-size justification or how uncertainty was handled in the trial’s planned analysis. The interval widths should be considered together with the outcome definitions, the completed-participant restriction, and the absence of a reported analysis plan.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants and not total events. They are illustrations computed from the observed effect, not the trial’s original design rationale. The registry lists the planning assumptions as a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial design assumptions are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm that the stated planning method estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column applies the same idea at a higher target chance of detection. These are design-planning targets, not probabilities that the completed trial’s result is correct. This is not observed power.

The rows using 100%, 75%, and 50% of the observed effect show how the planning count changes when the effect targeted for detection is smaller than the observed estimate. Smaller effects need more participants to detect under the same assumptions, so the entries increase as the targeted fraction decreases. This is especially relevant when an observed estimate from a small study is used as the basis for planning: an effect estimate can be uncertain, and using it without shrinkage may produce an optimistic planning illustration.

The calculations are not a reconstruction of the investigators’ original planning. They do not establish that the study had adequate power for its primary or secondary outcomes, and they do not replace information about the prespecified endpoint, expected variability, attrition assumptions, or planned analysis, none of which is reported in the registry record.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.910; pooled standard deviation σ = 2.590.
2. n = 2 × (1.96 + 0.842)² × 2.590² / -1.910² = 28.9, rounded up to 29 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
delta <- -1.91                      # observed difference in means
sigma <- 2.59                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4385888)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 29 (80% power), 39 (90% power)
 75% of observed effect: n per arm = 52 (80% power), 69 (90% power)
 50% of observed effect: n per arm = 116 (80% power), 155 (90% power)
power.t.test: 29.9 
Simulated power at n = 29 per arm: 0.789 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 record lists a primary outcome and secondary outcomes, but it does not report a complete statistical analysis plan. In particular, it does not state whether testing across outcomes was adjusted for multiplicity, whether a hierarchy of tests was prespecified, or whether secondary analyses were intended to be confirmatory or exploratory. The reported TNF-alpha p-value is unadjusted, so it should be read with the possibility of multiple testing in mind.

Multiplicity matters because each additional statistical test creates another opportunity to observe a result that looks unusual even when there is no underlying effect. An adjustment can control that concern, but no adjustment should be assumed when it is not described in the record. Conversely, the absence of a reported adjustment is not proof that none was conducted outside the registry; the analysis details are not reported in the registry record.

Missing-data handling is also not described. The primary endpoint is explicitly limited to children who completed the study, and the outcome summaries give 13 participants in each child group. The record does not report how many assigned participants lacked endpoint measurements, why measurements were missing, or whether the analysis followed intention-to-treat, per-protocol, or another population definition. No imputation strategy or sensitivity analysis is described. These gaps prevent assessment of how missing outcomes may have influenced the comparison.

The registry reports no analyses in its analysis listing. The group summaries and recalculated comparisons therefore do not offer the same transparency as a detailed analysis report with prespecified models, covariate handling, and diagnostic checks. The discrepancy indicator is false, but the registry still does not provide a sponsor-reported analysis set or methodological detail sufficient to determine whether the posted recalculations match an original analysis.

The original sample-size justification, interim analysis plans, and stopping rules are not reported in the registry record. These details should not be inferred from the separate planning illustrations based on observed effects. In combination, the missing analysis-plan and missing-data information mean that the results can be described at the summary-statistic level, while stronger claims about confirmatory inference remain unsupported by this record.

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.

The registry lists serious and other adverse event information separately for children and parents in each study group. For children assigned to restriction, 15 were listed at risk for serious adverse events and 15 for other adverse events; 0 were affected in each category, and deaths were 0. For children in usual consumption, 13 were listed at risk in each adverse-event category; 0 were affected in each category, and deaths were 0.

The parent groups are also listed: 15 at risk in each adverse-event category for restriction and 13 for usual consumption. The recorded affected counts are 0 for serious and other adverse events in both parent groups, and deaths are 0. These safety denominators are not the same presentation as the primary outcome counts, so the groups and outcome-specific populations should not be conflated.

No serious adverse event terms are listed. Zero recorded affected events in these groups means the registry reports none in the categories shown; it does not establish that every possible harm was assessed or that rare events can be ruled out. The record does not provide additional details about event collection, follow-up, or attribution beyond the posted figures.

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

The primary result describes a short-term comparison of mean change in TIR among children who completed the study. The estimated difference favors a larger mean change in the usual-consumption group numerically, but the interval includes zero and extends across a range of possible differences. The registry result therefore does not precisely establish a between-group difference in the primary endpoint.

This is not a test of whether low-calorie sweeteners prevent diabetes complications over the long term. The registry summary frames a broader motivation, but the posted primary measure is change in TIR over the intervention period. There is no reported long-term complication outcome in the result information. Nor does the primary outcome establish the effect of every source of low-calorie sweeteners, because the intervention was a behavioral instruction to avoid such sources during the study period.

The secondary TNF-alpha result is a separate biomarker comparison and should not be used to substitute for an uncertain primary result. A secondary difference does not show that the primary outcome changed, nor does it demonstrate a downstream health benefit or harm. The registry does not report a numerical visceral adiposity result, multiplicity handling, or a unified analysis of the outcomes.

The study is recorded as completed and randomized, but the primary result is limited to study completers, and the record does not explain missing outcomes. It also does not report the detailed statistical plan, measurement methods, or clinical thresholds for interpreting the size of a change. These constraints affect both the precision and the scope of interpretation.

The findings should therefore be read as descriptions of the posted group summaries and recalculated comparisons. They do not prove that restricting low-calorie sweeteners improves or worsens health, and they do not support medical advice. Their most defensible contribution is to characterize the observed short-term outcome estimates, their uncertainty, and the information gaps in the registry record.

17. Why This Trial Matters Statistically

This study illustrates why an outcome label and its operational description both matter. The primary endpoint is titled “Glycemic Variability,” but the outcome description identifies change in TIR. Readers need to know which construct was actually measured before interpreting an effect estimate. A concise registry label may not capture all of the measurement detail needed for a statistical or clinical interpretation.

It also illustrates the distinction between an estimated effect and its precision. The primary mean difference is a single summary, while its interval shows uncertainty around that estimate. The p-value alone cannot communicate the range of values compatible with the data, and it does not tell whether a difference is clinically important. Considering the estimate, interval, group variability, and outcome population together gives a more complete statistical reading.

The result also highlights the difference between primary and secondary evidence. A secondary biomarker result may be statistically distinct from zero while the primary outcome remains uncertain. Without a reported multiplicity plan, secondary p-values should not be granted the same confirmatory weight as a prespecified primary comparison. Missing results for another listed secondary outcome further limit any account of the full outcome pattern.

Finally, sample-size illustrations based on observed effects are useful for exploring planning scenarios, but they are not the same as the trial’s original design justification. In this record, the original rationale and analysis plan are not reported. Separating retrospective planning illustrations from prospective design assumptions helps prevent an observed result from being mistaken for evidence about the study’s intended power or rigor.

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 are specific to the information available for this trial. The primary outcome is reported only among children who completed the study, while the record does not explain missing outcome data or how the analysis population was defined. The outcome-specific counts are smaller than overall enrollment, but the record does not give participant flow details that would explain why.

The endpoint is labeled as glycemic variability but described as change in TIR. The registry does not report the target range, measurement technology, collection schedule, or details of how baseline and follow-up measurements were summarized. These omissions limit interpretation of what the measured change represents and how comparable it is across participants.

The registry does not describe who was masked, how allocation was generated or concealed, whether adherence to restriction was measured, or whether the analyses adjusted for baseline values. The original sample-size justification, full statistical analysis plan, and handling of multiplicity are also not reported. These are not evidence that a particular procedure was absent; they are information gaps in the registry record.

The posted TNF-alpha result is secondary and unadjusted, while visceral adiposity is listed without a numerical result. Safety summaries show no recorded affected events in the groups listed, but the record does not provide detailed methods for event ascertainment or follow-up. Taken together, these limitations favor a cautious reading of the posted descriptive comparisons and discourage generalizing beyond the measured outcomes, study period, and participants represented in the summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effects of Low-calorie Sweetened Beverage Restriction in Youth With Type 1 Diabetes — NCT04385888.
• Registry record last updated 2025-08-26; status last verified 2025-08.
• Results first posted 2025-08-26.
• 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

NCT04385888 is a completed randomized, single-masked, parallel behavioral study of low-calorie sweetener restriction in youth with type 1 diabetes. The restriction strategy involved avoiding low-calorie sweetened beverages and other sources for 12 weeks, while the comparison group continued usual consumption.

The primary outcome is described as change in TIR from baseline to weeks 11–12 and is measured in percent. The recalculated mean difference is -1.91, with an interval from -3.901 to 0.081 and an unadjusted p-value of 0.06. The primary result is limited to children who completed the study.

A secondary TNF-alpha result is posted; a numerical visceral adiposity result is not reported in the registry record. The record does not provide the original sample-size rationale, detailed analysis plan, multiplicity approach, or explanation of missing primary outcome data. These gaps constrain interpretation beyond the posted summary estimates.