Incisionless Treatment for Patients With Inadequate Weight Loss Following Roux-en-Y Gastric Bypass: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Incisionless Treatment for Patients With Inadequate Weight Loss Following Roux-en-Y Gastric Bypass (NCT00394212), a randomized phase 3 study. The primary outcome is Weight Loss (%).

2. Clinical Question

The clinical rationale in the registry is that the opening between the stomach pouch and intestine can become stretched after gastric bypass. The description proposes that a wider opening may allow food to pass more quickly and reduce fullness after eating. The trial evaluates whether an incisionless procedure designed to tighten that opening is associated with a different weight-loss outcome than a sham procedure. The proposed mechanism is a rationale for the intervention, not a result established by the primary endpoint.

The registry also lists outcomes for reaching specified excess weight loss thresholds and for weight stabilization. Those measures address different aspects of weight change from the continuous primary outcome, so they can add context but do not replace the primary comparison. The available results cover a 6-month timeframe.

3. Trial Design

The registry identifies RESTORe as a phase 3, randomized, double-masked, parallel-group study. Enrollment is recorded as 77. The two arm summaries list 50 participants for transoral suturing and 27 for sham endoscopy. These are the arm counts recorded with the posted outcome results; the registry record does not explain the allocation process or why the arm counts differ.

The intervention was transoral suturing of the dilated gastrojejunostomy. In the sham group, endoscopy was performed without suturing. Double masking is the recorded design description, but the registry record does not report who was masked or how masking was maintained. Details of sequence generation, concealment, procedural standardization, and masking assessment are not reported in the registry record.

The study started in 2006-11 and has a primary completion date of 2008-09. Its status is listed as terminated. The reason for termination and any consequences for recruitment or follow-up are not reported in the registry record. The posted primary result concerns weight loss at 6 months and uses an intention-to-treat population with last observation carried forward. The registry also records three secondary outcomes at 6 months.

The record does not describe the original sample-size justification, the planned statistical analysis in full, whether interim analyses took place, or whether the study stopped according to a prespecified rule. The planning illustrations associated with the posted results are separate from those unreported elements of the original design. They use the observed effect for illustrative calculations and cannot establish what assumptions guided the trial before it began.

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: Prior to enrollment, prospective candidates having provided informed consent were screened for eligibility during a formal 6 week screening period. Screening performed by a multidisciplinary team including surgeon and/or endoscopist, psychiatric professional and registered dietician.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT using Last Observation Carried Forward (LOCF)

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 Weight Loss (%), measured over 6 months.

The primary endpoint is percent weight loss at 6 months. The registry defines it as baseline weight minus 6-month weight, divided by baseline weight, then multiplied by 100. It is a continuous measure: each participant's weight change is represented on a percentage scale, and the posted group summaries report means and standard deviations.

Using a percentage of baseline weight expresses change relative to a participant's starting weight rather than only as an absolute weight change. A group mean summarizes the average observed percentage weight loss, while the standard deviation describes variation among individual values around that mean. These summaries provide information about both the average and the spread of outcomes; they do not show the full distribution or explain why participants' outcomes differed.

The endpoint is used to compare the groups' average weight change at the stated follow-up. It does not directly measure the proposed change in the gastrojejunostomy opening, fullness after eating, or passage of food. Those are part of the registry's rationale for the intervention, not the primary outcome itself. The 6-month timeframe also means the posted primary comparison addresses weight loss at that follow-up, not longer-term weight change.

The primary analysis population is recorded as intention-to-treat with last observation carried forward. This specifies how the registry says the primary endpoint was analyzed, but details about the amount and pattern of missing weight measurements are not reported in the registry record.

7. Results Posted in the Registry

• EndoCinch Suturing System:Transoral Suturing: mean 4.20 versus 1.90 on control; difference 2.30 (95% CI -0.17 to 4.77), standardized effect d = 0.43; z-test p = 0.068.

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.

Subjects Achieving 15% Excess Weight Loss (EWL)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • EndoCinch Suturing System:Transoral Suturing: 42.0% (21/50) versus 25.9% (7/27) on control; risk difference 16.1 percentage points (95% CI -5.4 to 37.5), risk ratio 1.62 (0.79–3.31); unadjusted two-proportion z-test p = 0.162.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EndoCinch Suturing System:Transoral Suturing and the control. The interval gives the range of effects that remain compatible with the data.

Subjects Achieving Weight Stabilization at 6 Months

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • EndoCinch Suturing System:Transoral Suturing: 96.0% (48/50) versus 77.8% (21/27) on control; risk difference 18.2 percentage points (95% CI 1.6 to 34.8), risk ratio 1.23 (1.00–1.52); unadjusted two-proportion z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for EndoCinch Suturing System:Transoral Suturing than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Subjects Achieving 20% Excess Weight Loss at 6 Months

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • EndoCinch Suturing System:Transoral Suturing: 34.0% (17/50) versus 14.8% (4/27) on control; risk difference 19.2 percentage points (95% CI 0.4 to 37.9), risk ratio 2.30 (0.86–6.14); unadjusted two-proportion z-test p = 0.071.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EndoCinch Suturing System:Transoral Suturing and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover threshold-based excess weight loss and weight stabilization at 6 months. Across the posted arm summaries, the direction of the comparisons is generally favorable to transoral suturing, while the strength of statistical evidence varies by outcome and by analysis. These measures give a broader view of the observed weight outcomes, but they are not interchangeable with the primary continuous measure of mean percent weight loss.

Some secondary comparisons have recalculated intervals that exclude zero, while others include zero; the registry's own tests also do not give identical inferential results to the recalculations. The analyses differ in method, and the posted summaries do not provide a single adjusted analysis integrating all endpoints. The secondary pattern can therefore be considered alongside the primary result, but it does not overturn or replace the primary comparison.

Unadjusted secondary findings carry less weight because examining multiple outcomes increases the opportunity for apparently notable results to arise by chance. This is a general statistical concern, not a statement that any particular secondary finding is false. The registry record does not report a multiplicity strategy, a hierarchy for testing outcomes, or which secondary outcomes were intended to be confirmatory. Without that information, individual secondary p-values should be treated as exploratory signals rather than as a set of independent confirmations.

The secondary measures may still be useful for understanding how the groups' observed outcomes varied across different definitions of weight change. Their interpretation remains limited by the 6-month follow-up, the modest group sizes, and the absence of reported details about missing data and analysis populations for each secondary endpoint. They do not establish longer-term outcomes or the mechanism described in the study rationale.

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

• Subjects Achieving 15% Excess Weight Loss (EWL)
• Subjects Achieving Weight Stabilization at 6 Months
• Subjects Achieving 20% Excess Weight Loss at 6 Months

9. Statistical Interpretation

10. Statistical Methods Explained

Two different statistical approaches appear in the primary result. The posted registry analysis is a Wilcoxon (Mann-Whitney) test. The accompanying recalculation treats the primary measure as continuous and compares the group means using the posted means, standard deviations, and arm sizes. These approaches answer related but not identical questions, so their p-values need not match exactly.

What does the mean difference describe?

The mean difference is the average percent weight loss in the suturing group compared with the average in the sham group. The recalculated estimate is 2.3 percentage points. A positive value indicates a higher mean percent weight loss in the suturing group under this contrast definition. It is an unadjusted comparison: it does not account for baseline covariates or other factors beyond the posted group summaries.

A mean is sensitive to the size of each observation, rather than only to its rank or whether it falls above or below another observation. The standard deviation describes the dispersion of observations around the mean. Here, the group standard deviations are 5.4 and 5.2. Those statistics help characterize the data, but they do not reveal distribution shape, outliers, or whether a normal approximation is a good description of the observed values.

Why use a Wilcoxon (Mann-Whitney) test?

The Wilcoxon (Mann-Whitney) test compares the ordering of observations across groups. In general, a rank-based procedure can be useful when an analysis is intended to rely less on assumptions about the exact distribution of a continuous outcome. Its interpretation is not simply a test of equal means in all circumstances; its behavior can reflect differences in distributions, including shifts and differences in spread. The registry reports the method and p-value but does not report additional details about the test's implementation or its assumptions.

The recalculated mean comparison is a different summary-based analysis. It makes the group mean contrast explicit and produces an interval around that contrast. Its p-value is unadjusted and should not be mistaken for the registry's own rank-based p-value. The closeness of the two p-values does not make the methods interchangeable.

How should the confidence interval be read?

A confidence interval is a range of values generated by a method that, over repeated studies under its assumptions, would cover the underlying parameter at the stated rate. It communicates uncertainty about the estimated mean difference. The recalculated interval includes zero, indicating that zero difference is among the values compatible with the interval. An interval is not a guarantee that the true effect lies inside it, and it does not give the probability that a particular value is true.

Interpretation depends on the analysis assumptions. The registry record provides group means, standard deviations, arm sizes, and the recalculated interval, but does not report a full account of diagnostics or modeling choices. The recalculation is not covariate adjusted and does not incorporate individual participant data.

What does intention-to-treat with last observation carried forward mean?

Intention-to-treat generally refers to analyzing participants in the groups to which they were assigned, regardless of whether they completed or adhered to the intervention. The registry says the primary population used this approach with last observation carried forward, or LOCF. LOCF fills a missing follow-up value using the participant's last recorded value. This can preserve a group assignment-based analysis, but it assumes that the carried-forward value is a suitable stand-in for the missing follow-up measurement. If weight would have changed after the last recorded measurement, LOCF may not represent that trajectory.

The registry record does not report the number of missing primary measurements, their timing, reasons for missingness, or alternative analyses of missing data. It is therefore not possible to judge how much the LOCF choice affected the result from the posted summaries alone.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. If a method assumes less variability than the data contain, uncertainty can be understated and inferential results can appear more decisive than warranted. For the continuous primary endpoint, the posted standard deviations show substantial variation, but the registry record does not report a specific over-dispersion assessment or model. This general concern should not be taken as evidence that a particular model assumption was violated in this trial.

For the binary secondary outcomes, the registry reports Fisher exact tests, while the recalculations use unadjusted risk differences and related summary measures. The exact test is designed for categorical count data; the recalculated contrasts describe differences in observed proportions. As with the primary outcome, those are distinct analyses. The registry does not report a multiplicity adjustment or a full plan specifying which secondary comparisons were confirmatory.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 2.3 percentage points, and its confidence interval extends from a value slightly below zero to a positive value. The interval therefore includes no difference and also allows a positive contrast. This range signals that the point estimate alone should not be read as a precise determination of the size of the group difference.

Precision depends on the amount of information in the data and their variability. The primary endpoint has reported standard deviations of 5.4 and 5.2, alongside arm counts of 50 and 27. The observed variability is large relative to the mean difference, which contributes to uncertainty in the estimated contrast. The interval captures that uncertainty under the recalculation's assumptions; it does not correct for possible bias from missing data, trial conduct, or selective reporting.

A confidence interval is more informative than a point estimate alone because it shows a range of effects compatible with the analysis. It should not be interpreted as assigning equal plausibility to every value in the range, and it is not a prediction interval for an individual participant's outcome. The interval also cannot establish clinical importance: the registry record does not provide a threshold for a meaningful between-group difference.

The registry's reported Wilcoxon analysis gives p = 0.066, while the unadjusted recalculation gives p = 0.068. The p-values indicate that the primary comparison does not provide strong evidence against the null under conventional reference standards, but they do not replace the interval's information about possible effect sizes. The registry does not report a confidence interval for its rank-based analysis, so the recalculated mean-difference interval should not be attributed to that analysis.

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 illustrations are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total enrollment targets or total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the listed fraction of the observed effect. These are planning calculations, not the trial's original design assumptions; those original assumptions are not reported in the registry record.

In plain language, an 80% power calculation asks how many participants per arm a hypothetical study would plan to enroll to have an 80% chance of detecting the specified effect under the calculation's assumptions. The 90% column uses a higher chance of detection, which generally requires more participants. For example, planning for 100% of the observed primary effect gives 85 participants per arm for 80% power and 113 participants per arm for 90% power.

The rows that plan for 75% and 50% of the observed effect use smaller target effects. Detecting a smaller difference is harder when other assumptions stay the same, so those scenarios require more participants per arm. The figures illustrate how the planning requirement changes as the assumed effect changes; they do not show what the trial actually had a chance to detect after its results were observed.

This is not observed power. It is a forward-looking planning illustration based on the observed effect and specified assumptions, not a measure of the strength or reliability of the completed trial's result. The registry record does not report the original sample-size justification, so these calculations should not be used to infer what enrollment was intended or whether the trial met its original design targets.

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 = 2.300; pooled standard deviation σ = 5.332.
2. n = 2 × (1.96 + 0.842)² × 5.332² / 2.300² = 84.3, rounded up to 85 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 <- 2.3                      # observed difference in means
sigma <- 5.33151635716019                     # 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(394212)
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 = 85 (80% power), 113 (90% power)
 75% of observed effect: n per arm = 150 (80% power), 201 (90% power)
 50% of observed effect: n per arm = 338 (80% power), 452 (90% power)
power.t.test: 85.3 
Simulated power at n = 85 per arm: 0.799 (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. Analyses Reported by the Sponsor

The registry's own primary analysis is the Wilcoxon (Mann-Whitney) comparison, with p = 0.066. The recalculated summary-statistic comparison of group means gives p = 0.068 and a mean difference of 2.3 percentage points. The recalculation uses the posted means, standard deviations, and arm sizes; it is a simple unadjusted analysis rather than a recreation of the rank-based test.

The small difference between these p-values is consistent with the fact that the analyses use different statistical methods. One evaluates ranks, while the other evaluates a mean contrast. They should therefore be reported as separate results, not blended or presented as though one confirms the other. The direction of the mean contrast favors the suturing group, but the recalculated confidence interval includes zero.

The registry record does not identify a discrepancy between the posted primary analysis and the recalculation. The registry's own analysis remains the trial's reported analysis, and the recalculation is supplementary context. The record does not provide enough detail to determine whether the rank-based procedure was the prespecified primary test or how it relates to a complete statistical analysis plan.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes or comparisons are tested. Even when each test uses the same nominal threshold, the chance of obtaining at least one apparently positive result can increase as more tests are considered. A prespecified hierarchy or adjustment can help manage that issue. The registry lists one primary outcome and three secondary outcomes, but a multiplicity adjustment or testing hierarchy is not reported in the registry record.

Consequently, secondary p-values should be read as unadjusted evidence for their individual comparisons, not as proof that the family of secondary outcomes collectively confirms an effect. The record does not say whether the secondary outcomes were confirmatory, exploratory, or selected after the results were known. The primary result should remain the central statistical comparison, with secondary results interpreted in the context of that outcome and the missing multiplicity information.

The primary population is described as intention-to-treat using last observation carried forward. That gives some information about how missing primary follow-up measurements were handled, but not about how many measurements were missing, when they became unavailable, or why. The registry record does not report sensitivity analyses using other missing-data assumptions. LOCF is not automatically conservative: depending on the actual course of outcomes after the last observed measurement, it can move estimates in either direction.

Analysis populations for the secondary outcomes are not reported in the registry record. Nor does the posted information explain whether participants who lacked a particular secondary measurement were excluded, imputed, or handled by another method. This limits the ability to compare secondary results with the primary intention-to-treat analysis on a like-for-like basis.

The full statistical analysis plan, interim analyses, and rules for handling protocol deviations are not reported in the registry record. These absences make it difficult to assess prespecification and the potential influence of analytic choices. They do not establish that analyses were inappropriate; they mark uncertainty that cannot be resolved from the posted record.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: adhesion-related intestinal obstruction (from prior surgery) (2.1%), pulmonary edema secondary to fluid overload (2.1%).

The serious adverse-event summaries report 2 affected participants among 48 at risk in the transoral suturing group and 0 among 29 at risk in the sham endoscopy group. The registry also lists other adverse events affecting 18 among 48 at risk in the suturing group and 10 among 29 at risk in the sham group. These are descriptive counts from the posted safety record and should be read with their group-specific at-risk denominators.

The listed serious-event terms are adhesion-related intestinal obstruction (from prior surgery) and pulmonary edema secondary to fluid overload, each recorded as 2.1%. The record does not provide enough detail to determine the timing, duration, severity grading, or causal relationship of these events to the study procedures. The term “from prior surgery” appears in the listed event description; it does not establish the full clinical context.

Deaths are not reported in the registry record. No comparative safety test or uncertainty interval is posted in the registry record reported for these event counts. Small event counts can provide limited precision, and a zero count in one group does not establish that an event is impossible or that the groups have equivalent safety. The summaries describe reported events; they do not support medical advice or a broad conclusion about safety outside this trial.

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

The posted primary result shows a higher mean percent weight loss at 6 months in the transoral suturing group than in the sham endoscopy group. The recalculated mean difference is 2.3 percentage points. However, the uncertainty interval includes zero, and the registry's own Wilcoxon analysis reports p = 0.066. The result does not establish a definitive difference in mean weight loss between the groups.

This does not mean that the groups were proven equivalent. A result that does not provide strong evidence against a no-difference model is not the same as evidence that any difference is absent. The interval allows a range of possibilities, and the available data do not identify the exact size of any underlying difference with high precision.

Nor does the result prove that the procedure's proposed mechanism occurred. The registry's rationale concerns tightening the opening between the stomach pouch and intestine and potentially slowing food passage. The primary endpoint measures weight loss; it does not directly measure opening size, food passage, or fullness. Those mechanistic outcomes are not reported in the registry record.

The findings are limited to the recorded study population, sham-controlled comparison, and 6-month timeframe. They do not establish longer-term weight change, outcomes with other procedures, or results in populations not described by the registry. The record lists the trial as terminated, but does not report the reason or enough information to assess how termination related to the posted results.

The secondary outcomes add context about threshold-based weight change and stabilization, but they involve multiple comparisons and no reported multiplicity strategy. They should not be treated as independent confirmation of the primary outcome. The available adverse-event counts are descriptive and likewise do not establish a comprehensive comparative safety profile.

18. Why This Trial Matters Statistically

This trial illustrates why an estimate, its uncertainty, and the method used to obtain it all matter. The observed difference in mean percent weight loss is positive, but the confidence interval includes zero. Reporting only the group means could make the contrast appear more conclusive than the interval supports; reporting only a p-value would conceal the range of plausible mean differences represented by the recalculation.

It also demonstrates that two reasonable-looking statistical summaries can answer different questions. The registry reports a rank-based test, whereas the recalculation compares means from summary statistics. Their p-values are close, but closeness does not make the estimands or methods identical. Transparent labeling helps readers distinguish the official reported analysis from an unadjusted recalculation.

The trial is also a useful example of the importance of planning assumptions. Illustrative sample-size calculations based on an observed effect are not the same as an original design justification. Their required enrollment varies with the effect targeted, and a smaller effect requires more participants under the stated assumptions. These calculations explain planning trade-offs without revealing the trial's original intent or its prospective ability to detect an effect.

Finally, multiplicity, missing-data handling, and status matter for interpretation. The primary outcome uses LOCF, but the extent of missingness is not reported. Multiple secondary outcomes are posted without a reported adjustment strategy, and the trial is listed as terminated without a reason. These gaps do not invalidate the results, but they define limits on how confidently the results can be generalized or treated as confirmatory.

19. Limitations

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

The registry record does not report the reason for termination, the original sample-size justification, or the full statistical analysis plan. It also does not describe interim analyses, allocation concealment, the randomization procedure, or who was masked. These details would help assess the trial's conduct and whether the reported analyses followed prespecified procedures.

The primary endpoint uses LOCF, but the number and timing of missing measurements and the reasons for missingness are not reported in the registry record. The consequences of this imputation cannot be evaluated from the posted summaries. The analysis populations and missing-data handling for the secondary outcomes are also not reported.

The primary follow-up is 6 months. Longer-term weight outcomes are not reported in the registry record, so persistence of any observed difference cannot be assessed. The primary measure is weight loss; the proposed change to the gastrojejunostomy opening and related mechanisms are not measured by that endpoint.

The trial includes a sham comparison and is recorded as double masked, but practical details about masking and the success of masking are not reported. The record also does not provide a clinical threshold for a meaningful difference in the primary endpoint. As a result, statistical uncertainty can be described, but the clinical importance of the estimated contrast cannot be judged from the registry record alone.

The posted safety summaries give counts, but not detailed event timing, severity, causality assessment, or comparative uncertainty. The secondary outcomes involve multiple analyses without a reported adjustment strategy. These limitations support cautious interpretation rather than a broad conclusion about the intervention or its effects beyond the reported outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Incisionless Treatment for Patients With Inadequate Weight Loss Following Roux-en-Y Gastric Bypass — NCT00394212.
• Registry record last updated 2016-09-21; status last verified 2012-10.
• Results first posted 2012-11-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

RESTORe is recorded as a phase 3, randomized, double-masked, parallel-group trial of transoral suturing versus sham endoscopy for people with inadequate weight loss or weight regain after Roux-en-Y gastric bypass. Enrollment is listed as 77, and the study status is terminated.

The primary outcome was mean percent weight loss at 6 months, analyzed in an intention-to-treat population using last observation carried forward. The registry reports a Wilcoxon (Mann-Whitney) p-value of 0.066. The unadjusted recalculation gives a mean difference of 2.3 percentage points, with an interval that includes zero.

Three secondary weight outcomes and adverse-event summaries are also posted. The reason for termination, original sample-size justification, full analysis plan, multiplicity strategy, and detailed missing-data information are not reported in the registry record.