Vibrant Capsule vs. Placebo for Patient Suffering From Constipation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vibrant Capsule vs. Placebo for Patient Suffering From Constipation (NCT05036369), a randomized na study. The primary outcome is CSBM 1 Success Rate.

2. Clinical Question

The study asks whether participants assigned to the Vibrant capsule differed from participants assigned to placebo in the proportion meeting the registry’s CSBM 1 success definition during treatment. The result is based on the registry’s mITT population and a binary outcome: each participant either met the success definition or did not.

The outcome relies on participants’ bowel-movement records and on the distinction between spontaneous and complete spontaneous bowel movements. A spontaneous bowel movement is defined as occurring at least 48h after laxative or rescue intake and without digital maneuver. A complete spontaneous bowel movement additionally involves a feeling of complete evacuation, as assessed by the participant.

This question is narrower than asking about every aspect of constipation or every experience during treatment. It concerns a specified change from the run-in period, sustained across a defined portion of treatment. The registry also lists outcomes related to straining, expanded CSBM success rates, and stool consistency, but those measures address different aspects of the study question.

3. Trial Design

The registry describes a prospective, randomized, multi-center, double-blinded clinical study comparing Vibrant capsule with placebo for chronic idiopathic constipation. The design is parallel: participants were assigned to one of the two groups rather than crossing between treatments. The study status is completed. The listed enrollment is 100, and the registry gives a start date of 2021-07-05 and a primary completion date of 2022-12-15.

The intervention descriptions distinguish a non-biodegradable active capsule from a softgel biodegradable placebo capsule. The placebo is described as visually similar to the active capsule. Both are described as administered twice a week. The record lists phase as NA and identifies the intervention type as a device.

The primary result is reported for the mITT population: 43 participants in the Active Capsule group and 53 in the Placebo group. Those outcome denominators should not be conflated with the listed overall enrollment or with the safety-group denominators. The safety results use 44 participants at risk in the Active Capsule group and 56 in the Placebo group. The registry record does not report further detail about how the mITT population was defined or how participants were assigned to that population.

The primary outcome timeframe is up to 8 weeks of treatment. Success is defined using change from the run-in period and requires the specified increase in weekly CSBMs during at least 6 of the 8 treatment weeks. The record lists secondary outcomes involving straining based on daily diaries, two expanded CSBM success measures, and change from baseline in stool consistency.

Although randomization and double blinding are recorded, the registry record does not report the allocation sequence method, concealment procedures, blinding assessment, site count, or detailed visit schedule. It also does not report the original sample-size justification, the protocol’s statistical analysis plan, or details of any interim analyses. These omissions limit how fully the conduct and planned analysis can be reconstructed from the registry record alone.

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: Following the consent process, subjects who met the study criteria started a run-in period of 2-4 weeks, during which they completed a daily eDiary with questions regrading their bowel movements and constipation symptoms.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT

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 CSBM 1 Success Rate, measured over up to 8 weeks of treatment.

The primary endpoint, CSBM 1 Success Rate, is a participant-level binary measure reported as a count of participants. Success means an increase from the run-in period of at least one weekly complete spontaneous bowel movement during at least 6 of the 8 weeks of treatment. The registry reports 24 participants meeting this definition among 43 in the Active Capsule group and 17 among 53 in the Placebo group.

The definition combines frequency, change from baseline, and persistence across treatment. A spontaneous bowel movement must occur at least 48h after laxative or rescue intake and without digital maneuver. A complete spontaneous bowel movement is one associated with the participant’s feeling of complete evacuation. Thus, this endpoint does not count every bowel movement; it focuses on events meeting the registry definitions and on whether the participant reaches the specified weekly pattern.

In general, a binary endpoint can summarize whether each participant crosses a clinically defined threshold, making the groups’ success proportions directly comparable. The threshold also makes the result easier to interpret than a measure of average change alone, but it discards information about outcomes among participants who do not meet the full success definition. A participant just short of the threshold and one with little change are both classified as not meeting success.

The endpoint is used as the primary measure of the study question, but the registry record does not report why this specific definition was selected, whether it was prespecified in a protocol, or whether it was chosen with input from participants or clinicians. The result therefore describes the posted endpoint as defined, not every dimension of constipation or treatment experience.

7. Results Posted in the Registry

• Active Capsule: 55.8% (24/43) versus 32.1% (17/53) on control; risk difference 23.7 percentage points (95% CI 4.3 to 43.2), risk ratio 1.74 (1.08–2.79); unadjusted two-proportion z-test p = 0.019.

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.

CSBM1 Expanded Success Rate,

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Capsule: 65.1% (28/43) versus 43.4% (23/53) on control; risk difference 21.7 percentage points (95% CI 2.2 to 41.2), risk ratio 1.50 (1.03–2.19); unadjusted two-proportion z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Active Capsule than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

CSBM2 Expanded Success Rate

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Capsule: 32.6% (14/43) versus 26.4% (14/53) on control; risk difference 6.1 percentage points (95% CI -12.2 to 24.5), risk ratio 1.23 (0.66–2.30); unadjusted two-proportion z-test p = 0.510.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active Capsule and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering straining, expanded CSBM success measures, and change from baseline in stool consistency. Posted comparison results are available for the two expanded CSBM success outcomes. The broader pattern is not uniform: one expanded success comparison has a positive risk-difference estimate with an interval excluding zero, while the other has an interval that includes zero. This contrasts with the primary CSBM 1 result, whose posted interval excludes zero. The registry record does not report results for the listed straining or stool-consistency outcomes.

These secondary outcomes relate to the primary result by assessing related but distinct definitions of bowel-movement success. The expanded CSBM measures are not interchangeable with the primary CSBM 1 definition. Differences in thresholds can lead to different classifications and estimates, even when outcomes concern related experiences. The secondary results can therefore add context, but they should not be treated as replications of the primary endpoint or as a replacement for it.

The secondary comparisons are reported with unadjusted p-values, and the registry record lists no reported analyses for them. The record does not say whether the analyses were prespecified, whether there was a testing hierarchy, or whether multiplicity was controlled. In general, when several outcomes are examined, some apparently notable results can arise by chance. Without a documented strategy for handling multiple comparisons, secondary findings carry less weight than the primary result and are better regarded as supportive or exploratory rather than decisive.

The overall pattern should be read with both consistency and uncertainty in mind. The presence of a positive result on one related endpoint does not establish that all aspects of bowel function changed in the same way. Nor does a less conclusive secondary comparison negate the primary comparison. Each result concerns its own definition and precision. Because several listed outcomes lack posted results, the registry record offers only a partial account of the secondary outcome pattern.

In general, secondary endpoints can help show whether a primary finding aligns with other measures, while also broadening the number of statistical questions. Here, the posted results provide some additional information about expanded CSBM definitions, but incomplete reporting and the absence of documented multiplicity methods constrain how strongly those findings can be integrated with the primary result.

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

• Straining Based on the Subject's Assessment Recorded in Daily Diaries
• CSBM1 Expanded Success Rate,
• CSBM2 Expanded Success Rate
• Change From Baseline in Stool Consistency

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants are counted as meeting or not meeting the CSBM 1 success definition. For a binary endpoint, the group result can be expressed as a proportion, and a risk difference compares those proportions by subtracting the comparator proportion from the intervention proportion. The posted comparison reports a risk difference of 0.237. This is an absolute contrast on the proportion scale, rather than a relative measure such as a risk ratio.

The posted group counts are 24 of 43 for Active Capsule and 17 of 53 for Placebo. The comparison also reports group proportions of 0.558 and 0.321, respectively. These are presented as registry results; no additional values need to be derived from the counts to interpret the posted comparison. A risk difference is often useful because it describes the size of the contrast in the same units as the outcome proportions. In general, it can be compared with a threshold for meaningful difference if such a threshold has been defined, but the registry record does not report one.

The risk difference is accompanied by a confidence interval from 0.043 to 0.432. In general, a confidence interval expresses uncertainty about an estimate under the assumptions of the method used. It is not a guarantee that the true effect lies in that particular interval, and its width reflects both the observed data and the statistical procedure. The registry record does not identify the exact procedure used to construct this interval, so it is not possible to assess details such as whether it used a particular score-based or approximation method.

The p-value for the primary comparison is 0.019 and is described as unadjusted in the registry results. In general, a p-value measures how unusual data at least as discordant with a null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, nor a measure of the clinical importance of an estimate. Because the registry record does not report the test method or the trial’s prespecified analysis plan, the p-value should be treated as a posted unadjusted statistic rather than as a complete account of the inferential procedure.

Other relative measures are posted as well: the risk ratio is 1.74, with a confidence interval from 1.084 to 2.794, and the odds ratio is 2.675, with a confidence interval from 1.162 to 6.157. These express the contrast on different scales. A risk ratio compares proportions, whereas an odds ratio compares odds. In general, odds and risks are not interchangeable, and an odds ratio can appear farther from one than the corresponding risk ratio when outcomes are common. For this reason, the absolute risk difference is a useful companion to the relative measures. No one scale alone conveys every aspect of the comparison.

Randomization is recorded, which in general is intended to balance measured and unmeasured characteristics between groups on average. Double blinding is also recorded and can reduce some forms of influence on participant experience or outcome assessment. Those design labels do not establish that allocation was concealed or that blinding was maintained; those details are not reported in the registry record. Nor does the registry record describe stratification, adjustment variables, or the exact randomization procedure.

The primary population is mITT. In general, an intention-to-treat approach analyzes participants according to randomized assignment, while modified intention-to-treat approaches may apply additional inclusion criteria. The precise meaning of mITT varies across studies. Here, the registry record does not report the population definition, reasons for exclusion, or how missing endpoint information was handled. It would therefore be inappropriate to assume a particular mITT rule or to infer that all randomized participants contributed to the primary comparison.

Binary outcome data can also be analyzed with models that adjust for covariates or account for other features of the design. The registry record does not report whether the primary result came from an unadjusted test, a regression model, or another method. The displayed risk difference and other measures describe the comparison, but they do not reveal all modeling decisions. In general, adjustment can change estimates and uncertainty, particularly when prespecified factors are included, so the absence of an analysis description matters when assessing reproducibility.

The record lists no reported analyses for the secondary outcomes. It also does not report whether there were interim analyses, how any multiplicity was handled, or whether the listed outcomes were ordered in a testing hierarchy. The absence of those details does not mean that no such methods were used; it means they are not reported in the registry record. In general, examining several outcomes increases the chance that at least one result may appear noteworthy by chance, so interpretation should account for the number and status of comparisons.

The planning illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The detectable effect is set to a stated fraction of the observed effect. These are general planning assumptions attached to the illustrations, not confirmed features of the original trial design. The trial’s original sample-size assumptions and justification are not reported in the registry record.

Over-dispersion is a concern for certain count outcomes when variability exceeds what a simple model expects. In general, modeling that extra variability can affect standard errors and confidence intervals. The primary endpoint is reported as a binary participant count, not a count of repeated bowel movements, and no dispersion estimate is listed. Consequently, over-dispersion is not a reported feature of this primary comparison. The registry record does not provide enough methodological detail to evaluate further model assumptions.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.237, and its 95% confidence interval ranges from 0.043 to 0.432. The interval is wholly on the positive side of zero, so the posted interval is consistent with a higher success proportion in the Active Capsule group under the reported comparison. At the same time, the interval spans a range of possible differences, which means the point estimate should not be treated as known without uncertainty.

In general, a confidence interval summarizes the precision of an estimate under the assumptions of the method used. A narrower interval indicates greater precision on the relevant scale; a wider interval indicates more uncertainty. Precision depends on factors such as the amount of information in the data and the variability of the outcome. The registry record does not report the exact interval method or a prespecified threshold for a difference considered important, so the interval cannot be translated into a judgment about clinical importance from the registry statistics alone.

The primary result includes 43 participants in the Active Capsule group and 53 in the Placebo group. These denominators help explain why the interval is not a single precise value: the estimate is based on a limited set of participant outcomes. The listed enrollment is 100, but the primary analysis denominators differ from the overall enrollment. The record does not explain the population flow or the reasons for the differing denominators, so the consequences of missing or excluded participants cannot be assessed from the posted summary.

The secondary comparisons also illustrate why interval estimates matter: their precision varies, and the evidence does not have the same pattern across outcomes. The registry record does not report multiplicity adjustment or a hierarchy for those tests. Accordingly, a confidence interval for an individual secondary contrast should not be read as if it were the only comparison undertaken. The primary interval is the clearest posted estimate for the stated primary question, but the full inferential context remains incompletely described.

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 expressed as participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants in each arm under the listed assumptions for a calculation with 80% power to detect the selected effect. The 90% power column gives the corresponding per-arm number for 90% power. In general, power is the probability that a specified analysis would meet its statistical criterion if the assumed effect were present and the model assumptions held. It is a planning concept, not a measure of how likely the study’s conclusion is to be correct.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the required sample size. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise similar assumptions. The much larger planning figures for a smaller fraction of the observed effect reflect that relationship. They are illustrations anchored to this trial’s observed effect, rather than evidence that the study was originally designed around those assumptions.

These figures are not observed power. They do not describe what the completed study achieved, and they do not repair limitations in the posted analysis or explain why the original enrollment was selected. The registry record does not report the trial’s original power target, significance procedure, allowance for loss to follow-up, or anticipated effect size. The planning display should therefore be read as a sensitivity illustration: it shows how sample-size requirements change across assumed effects and power targets under the stated planning conditions.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.321; treatment proportion p₁ = 0.558; average p̄ = 0.439.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7019 = 1.3757.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6815 = 0.5736.
4. n = (1.3757 + 0.5736)² / (0.2374)² = 67.4, rounded up to 68 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.320754716981132                          # control proportion
p1 <- 0.558139534883721                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(5036369)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 68 (80% power), 90 (90% power)
 75% of observed effect: n per arm = 119 (80% power), 159 (90% power)
 50% of observed effect: n per arm = 262 (80% power), 350 (90% power)
power.prop.test: 67.4 
Simulated power at n = 68 per arm: 0.797 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and several secondary outcomes, but it does not report how the study addressed multiplicity. Multiplicity arises when more than one statistical comparison is made: without an adjustment or a prespecified testing sequence, the chance of at least one apparently notable result can increase. The posted primary p-value is 0.019, and the available secondary p-values are unadjusted. The record does not say whether these values were adjusted elsewhere or whether a formal testing hierarchy was specified.

The registry lists four secondary outcome descriptions, while posted comparison results are available for two expanded CSBM success measures. Results for straining based on daily diaries and change from baseline in stool consistency are not reported in the registry record. The record also lists no reported analyses for the secondary outcomes. These omissions prevent a complete assessment of the planned outcome family and of whether all conducted secondary analyses are represented.

The primary population is labeled mITT, but its inclusion criteria are not reported in the registry record. The record does not explain how participants who lacked an outcome assessment were handled, whether imputation was used, or whether sensitivity analyses assessed missing-data assumptions. Missing data can affect both the estimated group contrast and its uncertainty, particularly when the likelihood of missingness differs between groups or is related to the outcome. Without participant-flow detail and missing-data methods, the direction or size of any such influence cannot be determined.

The registry does not report the original statistical analysis plan, the prespecified handling of protocol deviations, or whether interim analyses occurred. It also does not give the test method used for the primary p-value or confidence interval. These are not evidence that the study lacked appropriate procedures; they are limits on what can be verified from the registry record. A fuller account would be needed to evaluate whether the analyses followed prespecified decisions and how robust the results are to alternative assumptions.

Accordingly, the primary finding can be interpreted as the posted comparison for the named mITT endpoint, but not as a complete statistical audit of the trial. The lack of documented multiplicity, missing-data, and analysis-population procedures leaves important questions unresolved, especially for interpreting secondary findings and the scope of the primary inference.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalized due to bleeding from the catheter port (1.8%).

The safety results use groups of 44 participants at risk in the Active Capsule group and 56 in the Placebo group. The registry reports 0 serious adverse events in the Active Capsule group and 1 in the Placebo group. Deaths are reported as 0 in each group. Other adverse events are reported for 16 participants in the Active Capsule group and 11 in the Placebo group.

The registry lists “Hospitalized due to bleeding from the catheter port” as a serious adverse-event term, with 1.8% shown for the term. The summary does not provide enough detail to establish the timing, clinical course, relatedness to the intervention, or whether there were other serious-event terms. The group counts alone do not establish causation, and they should not be interpreted as a definitive comparison of safety.

In general, rare events are difficult to characterize precisely when participant counts are limited. A difference in observed event counts can reflect chance, differences in follow-up, or other factors, as well as possible treatment-related effects. The registry record does not report exposure-adjusted analyses, event adjudication methods, or detailed adverse-event definitions. These figures describe the posted safety counts; they do not by themselves establish the overall safety profile of either capsule.

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

The primary result describes a difference in the proportion of participants meeting a specific CSBM 1 success definition during up to 8 weeks of treatment. The registry reports 24 of 43 participants meeting the definition in the Active Capsule group and 17 of 53 in the Placebo group, with a posted risk difference of 0.237 and a 95% confidence interval from 0.043 to 0.432. The unadjusted p-value is 0.019. These figures summarize the recorded comparison and its statistical uncertainty.

They do not answer every question about the intervention or the condition. The endpoint counts participants who reach a specified threshold; it does not describe the full distribution of bowel-movement changes, every symptom, the quality of life, or whether changes persist beyond the treatment timeframe. The registry record does not report long-term outcome results. It also does not report all the listed secondary results, so the posted primary result cannot stand in for those unreported measures.

A statistically notable comparison does not by itself establish the size or importance of a benefit to participants. The risk difference is an estimate, and its confidence interval indicates uncertainty about the magnitude. The registry record does not report a threshold for a clinically meaningful difference, nor does it provide the context needed to judge how the outcome relates to participants’ priorities. The result should not be treated as a guarantee of an individual outcome.

The randomized, double-blinded description is relevant to study design, but the registry record does not report detailed allocation procedures, population flow, missing-data handling, or the full statistical plan. Those limitations affect how fully the result can be independently assessed. In addition, the unadjusted secondary results require caution because the record does not describe a multiplicity strategy.

The safety counts are also descriptive. There was 1 reported serious adverse event in the Placebo group and none in the Active Capsule group, with 0 deaths in each group, but these counts alone cannot establish whether an event was caused by an intervention or whether the groups differ reliably in safety. Overall, the record supports a precise description of the posted outcomes, while leaving broader questions about clinical importance, completeness, and generalizability unresolved.

17. Why This Trial Matters Statistically

This trial illustrates why the definition of a binary endpoint matters. CSBM 1 success is not simply a count of bowel movements: it combines a change from run-in, a weekly threshold, a complete-evacuation requirement, and persistence during at least 6 of the 8 treatment weeks. Those features determine which participants count as successes. Statistical interpretation must therefore begin with the endpoint definition rather than with a p-value alone.

It also illustrates the value of reporting an absolute contrast alongside relative measures. The posted risk difference of 0.237 is on the scale of proportions and is accompanied by a confidence interval. The relative measures provide another view of the same comparison, but they answer a different scale-based question. Reading estimates together with their intervals helps distinguish the observed point estimate from the range of values compatible with the data and the method.

The trial is also a useful example of the limits of registry summaries. The registry records randomization, double blinding, an mITT population, and a completed study, but does not report key analytic details such as the population definition, missing-data handling, multiplicity strategy, or original sample-size justification. These omissions do not erase the posted results, but they restrict independent assessment of how the results were produced and how fully the analyses reflect prespecified plans.

Finally, the planning illustrations demonstrate how assumed effect size influences sample-size requirements. Planning for a smaller fraction of an observed effect requires more participants per arm under the listed assumptions. Such illustrations can aid statistical reasoning, but they cannot reconstruct the original design rationale when that rationale is not reported. Keeping these distinctions clear helps prevent a post hoc planning calculation from being mistaken for evidence about the study’s original design or its observed power.

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.

The posted primary comparison is based on the mITT population, but the registry record does not define that population or explain why the primary denominators differ from the listed enrollment. Without participant-flow information, it is not possible to assess exclusions, incomplete assessments, or the potential influence of missing outcomes. The record also does not report imputation or sensitivity analyses.

The primary endpoint uses a threshold-based definition over up to 8 weeks. This supports a clear participant-level success classification, but it does not show the full range of outcomes or how close participants were to the threshold. The record does not report additional detail about the distribution of CSBM changes or whether results differed across the treatment period.

The study is described as multi-center, but the registry record does not report the number or characteristics of sites. It also does not report participant characteristics, subgroup results, adherence, or treatment exposure in sufficient detail for assessing how representative the analyzed groups were or whether results varied across settings. Generalizability beyond the enrolled population therefore cannot be established from the posted summary.

Several secondary outcomes are listed, but results are posted for only two expanded CSBM success measures. Straining and stool-consistency results are not reported in the registry record. The record does not document a multiplicity plan or distinguish confirmatory from exploratory secondary analyses. This limits the weight that can be placed on individual secondary findings.

The original sample-size justification, statistical analysis plan, test methods, handling of protocol deviations, and interim-analysis procedures are not reported in the registry record. The posted confidence intervals and unadjusted p-values can be described, but these omissions prevent a complete assessment of prespecification and analysis robustness. The planning illustrations use explicit assumptions, yet they do not explain the original enrollment target.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Vibrant Capsule vs. Placebo for Patient Suffering From Constipation — NCT05036369.
• Registry record last updated 2024-07-09; status last verified 2023-07.
• Results first posted 2024-07-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, prospective, randomized, multi-center, double-blinded, parallel study of Vibrant capsule versus placebo for chronic idiopathic constipation. Listed enrollment is 100, and the primary outcome is CSBM 1 Success Rate in the mITT population, assessed over up to 8 weeks of treatment.

The primary comparison reports 24 of 43 participants meeting success in the Active Capsule group and 17 of 53 in the Placebo group. The posted risk difference is 0.237, with a 95% confidence interval from 0.043 to 0.432 and an unadjusted p-value of 0.019. Secondary outcomes include measures of straining, expanded CSBM success, and stool consistency; only two expanded CSBM comparisons have posted results.

The safety summary reports 0 serious adverse events in the Active Capsule group and 1 in the Placebo group, with 0 deaths in both groups. Important details about missing data, multiplicity, the mITT definition, and the original statistical plan are not reported in the registry record. The posted statistics therefore support a description of the recorded results, with those reporting limits in view.