Trial of Linaclotide in Patients With Irritable Bowel Syndrome With Constipation (IBS-C): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Linaclotide in Patients With Irritable Bowel Syndrome With Constipation (IBS-C) (NCT00938717), a randomized phase 3 study. The primary outcome is Abdominal Pain and Complete Spontaneous Bowel Movement (APC) Responder, 9 Out of 12 Weeks.

2. Clinical Question

The primary outcome combines bowel movement frequency and abdominal pain improvement rather than evaluating either feature alone. To qualify, a patient had to meet the specified bowel movement criteria and have a decrease of at least 30 percent in abdominal pain score during a qualifying week, with the combined criteria met for at least 9 out of the first 12 treatment weeks. The trial’s registry record describes a 26-week treatment study, while this primary comparison concerns change from baseline to Week 12.

The central statistical question is about the proportion meeting that joint definition in each randomized group and the uncertainty around the between-group comparison. It is not a comparison of every symptom or every treatment week separately. The secondary outcomes cover other bowel and symptom measures, but they do not replace the primary responder question.

3. Trial Design

This was a phase 3, randomized, double-blind, placebo-controlled, parallel-group trial of oral linaclotide in patients with IBS-C. The registry reports quadruple masking. The study evaluated linaclotide against matching placebo over 26 weeks, with the primary efficacy outcome assessed from baseline to Week 12. The registry lists 805 randomized patients.

The primary efficacy population was defined by having at least one postrandomization entry for the primary efficacy assessment. The registry reports that 804 patients met that condition and were included in the Intent to Treat (ITT) Population. An observed-cases approach was used for missing postbaseline data. The primary result therefore reflects available postbaseline assessment records under that approach, rather than an imputation procedure described in the registry.

The randomized arm summaries report 403 patients for placebo and 401 for linaclotide for the primary outcome. For the adverse-event summaries, the at-risk figures are 403 for placebo and 402 for linaclotide. The registry does not report the reason that those safety denominators differ from the primary outcome denominators.

The registry record identifies the sponsor as Ironwood Pharmaceuticals, Inc., and the study status as completed. It records a start date of 2009-07 and a primary completion date of 2010-09. The registry record does not report the trial’s original sample-size assumptions or a detailed protocol for the statistical analyses. Those omissions limit what can be concluded about how the original design was planned, even though the posted outcome summaries allow comparisons of the observed groups.

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: Patients went through a 14 to 21 day Pretreatment Period during which the patients provided qualifying bowel habit and symptoms, and rescue medicine usage information through an interactive voice response system (IVRS). All randomized patients needed an abdominal pain score ≥ 3.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 805 patients were randomized to treatment. 804 patients had at least 1 postrandomization entry of the primary efficacy assessment and were included in the Intent to Treat (ITT) Population. An observed-cases approach to missing postbaseline data was applied.

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 Abdominal Pain and Complete Spontaneous Bowel Movement (APC) Responder, 9 Out of 12 Weeks, measured over Change from Baseline to Week 12.

The primary endpoint is the number of participants meeting the abdominal pain and complete spontaneous bowel movement (APC) responder definition for at least 9 out of 12 weeks. It is a binary outcome at the participant level: each person either meets the combined responder definition or does not. The outcome is assessed from baseline to Week 12.

A qualifying week required at least 3 complete spontaneous bowel movements (CSBMs), an increase of at least 1 CSBM from baseline, and a decrease of at least 30 percent in abdominal pain score from baseline. The abdominal pain score assesses the patient’s worst abdominal pain in the past 24 hours on an 11-point scale from 0-10, where 0 represents no pain and 10 represents very severe pain. A spontaneous bowel movement (SBM) is defined as one occurring without laxative, enema, or suppository use on either the calendar day of the movement or the day before. A CSBM is an SBM associated with a sense of complete evacuation.

As a general statistical point, a combined responder outcome can capture whether a participant meets several clinically relevant criteria together, rather than showing a change in only one measure. It also simplifies a multidimensional response into a yes-or-no classification. That simplification makes the result easier to interpret as a proportion of responders, but it does not describe the degree of improvement among people who fail to meet every part of the definition.

7. Results Posted in the Registry

• Linaclotide: 12.7% (51/401) versus 3.0% (12/403) on control; risk difference 9.7 percentage points (95% CI 6.1 to 13.4), risk ratio 4.27 (2.31–7.89); unadjusted two-proportion z-test p = <0.001.

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.

12-Week Complete Spontaneous Bowel Movement (CSBM) Frequency

• 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:
  • Linaclotide: mean 2.24 versus 0.70 on control; difference 1.54 (95% CI 1.21 to 1.87), standardized effect d = 0.64; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

12-Week Spontaneous Bowl Movement (SBM) Frequency

• 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:
  • Linaclotide: mean 4.02 versus 1.31 on control; difference 2.71 (95% CI 2.21 to 3.21), standardized effect d = 0.75; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

12-Week Change in Stool Consistency

• 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:
  • Linaclotide: mean 1.91 versus 0.61 on control; difference 1.30 (95% CI 1.13 to 1.47), standardized effect d = 1.18; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover bowel movement frequency, stool consistency, straining, abdominal pain, abdominal discomfort, bloating, and responder definitions for CSBMs. The registry lists 10 secondary outcomes, while the detailed numerical summaries available in this record cover CSBM frequency, SBM frequency, and stool consistency. Across those posted numerical summaries, the direction of change favors linaclotide relative to placebo. They add context about symptom dimensions related to the combined primary responder outcome, without measuring the exact same joint response.

The secondary measures are related to the primary question because bowel movement frequency and associated symptoms contribute to the overall IBS-C experience. However, a mean change in a symptom measure is not equivalent to the proportion meeting the primary responder criteria. The primary definition requires a repeated combination of bowel movement and abdominal pain thresholds; a secondary mean can reflect a group average without indicating how many people met that combination.

The reported secondary p-values are unadjusted. As a general statistical point, testing multiple outcomes creates more opportunities for apparently strong results to arise by chance, even when each individual test uses a conventional significance threshold. Without a reported multiplicity strategy, the secondary p-values should be treated as exploratory or supportive rather than as a set of independently confirmed conclusions. The registry record does not report whether a formal multiplicity adjustment or hierarchical testing plan was used.

The secondary results can therefore be read as evidence that the observed symptom changes were directionally consistent across the detailed measures, while keeping the primary endpoint distinct. They do not establish that every listed secondary outcome met a prespecified inferential standard, nor do they resolve questions about multiplicity or missing data across outcomes.

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

• 12-Week Complete Spontaneous Bowel Movement (CSBM) Frequency
• 12-Week Spontaneous Bowl Movement (SBM) Frequency
• 12-Week Change in Stool Consistency
• 12-Week Change in Severity of Straining
• 12-Week Change in Abdominal Pain Score
• 12-Week Change in Abdominal Discomfort
• 12-Week Change in Bloating
• Complete Spontaneous Bowl Movement (CSBM) Responder for 6 Weeks Out of 12 Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result concerns a binary participant outcome: meeting or not meeting the APC responder definition. The reported group counts and denominators describe the observed responder proportions. A risk difference compares those proportions by subtraction, while an odds ratio compares the odds of response between groups. The posted recalculation is unadjusted; the registry’s reported analysis uses a Cochran-Mantel-Haenszel method and reports an odds ratio.

What does an odds ratio describe?

As a general statistical explanation, an odds ratio compares the odds of an outcome in one group with the odds in another. An odds ratio above 1 indicates higher odds in the group named in the comparison, relative to the comparator, when the event is coded as response. It does not mean that the probability of response is multiplied by that value. Odds and probabilities are related but are not interchangeable, especially when outcomes are not rare. The reported odds ratio is an association measure for the trial groups, not a direct measure of absolute benefit for an individual.

Why are two estimates reported?

The registry reports the sponsor’s Cochran-Mantel-Haenszel odds ratio, while the recalculation gives simple unadjusted measures from the posted summary statistics. They address the same broad comparison but need not have identical numerical values because the measure and analysis approach differ. The risk difference is an absolute contrast in proportions; the odds ratio is a relative contrast in odds. Neither measure alone communicates all aspects of the outcome. The confidence intervals help convey the uncertainty associated with each estimate.

What does a confidence interval add?

As a general explanation, a confidence interval gives a range of values compatible with the observed data under the specified statistical procedure. A narrower interval indicates greater precision for that estimate; a wider interval indicates more uncertainty. A confidence interval is not a guarantee that the true effect lies within the particular reported range, and it does not describe variation in individual responses. Its interpretation depends on the analysis and assumptions used to construct it.

How should the secondary continuous outcomes be understood?

The posted secondary summaries include least-squares means and standard errors for changes from baseline. A least-squares mean is a model-based group mean; its precise interpretation depends on the model used. The registry record does not report enough detail to reconstruct those models. A standard error describes uncertainty in an estimated mean, rather than the spread of individual patient measurements. The posted recalculations compare the least-squares means as unadjusted mean differences. For those recalculations, the pooled standard deviation is approximate, and the resulting standardized effects are also approximate. They should not be mistaken for fully specified model-based estimates.

As a general statistical point, continuous outcomes preserve more information about the amount of change than a responder threshold does. A binary responder outcome is easier to summarize as a proportion, but its result can depend on the chosen thresholds. For these reasons, the combined primary endpoint and the separate continuous symptom measures answer related but not identical questions.

Why does over-dispersion matter?

As a general statistical explanation, a model that assumes a particular degree of variability can understate uncertainty if the actual data are more variable than that assumption allows. This is often described as over-dispersion. The registry record does not report an over-dispersion assessment or identify a count-model analysis for the primary endpoint. The primary outcome is reported as a participant count, so an explanation of over-dispersion is general context rather than a claim that it affected this trial.

The registry indicates that observed cases were used for missing postbaseline primary efficacy data. This means the primary efficacy summary was based on available postbaseline entries under the stated approach. A missing-data method can affect both the analysis population and the interpretation of the estimate; without additional analysis details, the extent of any effect cannot be quantified. No assumption about why data were missing or how missingness related to outcome should be made from this record alone.

Finally, a small p-value does not by itself establish the magnitude, precision, or broader relevance of a result. The effect estimate, its interval, the endpoint definition, analysis population, and missing-data handling all matter. General statistical concepts help explain those features, but they do not fill in aspects of the trial’s statistical plan that are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary odds ratio is 4.65, with a 95% confidence interval from 2.44 to 8.84. The interval is entirely above 1, consistent with the reported direction of higher odds of meeting the APC responder definition in the linaclotide group than in the placebo group. Its width also shows that the precise size of the odds contrast remains uncertain: values across a substantial range are compatible with the reported analysis.

The unadjusted recalculation reports a risk difference of 0.097, with a confidence interval from 0.061 to 0.134. This interval expresses uncertainty on the absolute-difference scale, not the odds-ratio scale. The recalculated odds ratio is 4.748, with a confidence interval from 2.491 to 9.051. Because the sponsor’s analysis and the simple recalculation use different approaches, their intervals should be interpreted with their respective estimates rather than treated as interchangeable.

As a general statistical explanation, a 95% confidence interval describes the long-run coverage property of a method under its assumptions. It is not a range containing 95% of individual patient outcomes and is not a probability statement about the fixed true effect after the data have been observed. Interval width depends on the amount and pattern of information in the data and on the method used.

The posted intervals support a direction of difference, but they do not remove uncertainty about the magnitude that would be observed in other settings. The registry does not report confidence intervals for the serious adverse event counts in the safety summary. The intervals for the primary result should not be used to infer precision for safety outcomes or for secondary outcomes that have different measures and analyses.

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 table and curve are illustrations based on observed effects, not the trial’s original design calculation. The listed 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 stated fraction of the observed effect. The registry record does not report the original sample-size assumptions used to plan this trial.

For these binary and continuous outcomes, the entries are participants per arm, not a combined total. The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions if that effect were real. The 90% power column gives the corresponding planning quantity for a 90% chance under those assumptions. These are planning concepts, not guarantees about a future study.

Rows planning for 100%, 75%, and 50% of the observed effect show how the illustration changes when the effect to detect is smaller. Smaller effects need more participants for the same target power under the stated assumptions. The values depend on the observed effect and the simplified planning framework, so they should not be treated as a re-creation of the trial’s design or as universal sample-size requirements.

This is not observed power. The figures do not measure the probability that the completed trial detected an effect after its results were known. They are prospective planning illustrations, and their assumptions may not match the original design, which is not 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.030; treatment proportion p₁ = 0.127; average p̄ = 0.078.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3803 = 0.7454.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3740 = 0.3148.
4. n = (0.7454 + 0.3148)² / (0.0974)² = 118.5, rounded up to 119 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 <- 0.0297766749379653                          # control proportion
p1 <- 0.127182044887781                          # 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(938717)
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 = 119 (80% power), 159 (90% power)
 75% of observed effect: n per arm = 181 (80% power), 242 (90% power)
 50% of observed effect: n per arm = 338 (80% power), 452 (90% power)
power.prop.test: 118.5 
Simulated power at n = 119 per arm: 0.843 (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. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis uses the Cochran-Mantel-Haenszel method and gives an odds ratio of 4.65, with a 95% confidence interval from 2.44 to 8.84 and p < 0.001. The posted recalculation uses the arm-level summary counts to produce an unadjusted risk difference and an unadjusted odds ratio. It gives an odds ratio of 4.748, with a confidence interval from 2.491 to 9.051, and an unadjusted p-value of <0.001.

The recalculated estimates are useful as a transparent check based on the posted summaries, but they do not reproduce every feature of the sponsor’s analysis. The risk difference is a different effect measure from the odds ratio, and an unadjusted calculation is not the same analysis as the reported Cochran-Mantel-Haenszel procedure. The estimates are broadly consistent in direction and scale, while their small numerical differences are not evidence by themselves of a contradiction.

The registry record does not flag a discrepancy between the reported analysis and the recalculation. The sponsor’s reported analysis remains the trial’s own analysis; the recalculation is a supplementary, unadjusted reading of the posted group summaries. The registry does not provide additional detail on the stratification or other implementation choices for the reported method.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity adjustment, a hierarchy of primary and secondary tests, or a family-wise error strategy. It also does not report whether interim analyses were planned or conducted. These omissions matter because testing several outcomes can increase the chance of at least one statistically significant result under a collection of null hypotheses. The primary endpoint is identified, but the handling of statistical error across the full outcome set is not described in the registry record.

The record lists 14 outcome measures and reports 10 secondary outcomes. The available secondary results should be interpreted with that broader set of outcomes in mind. Unadjusted p-values do not account for the number of comparisons, and nominal significance alone cannot establish that each secondary finding was confirmatory. The registry record does not report whether the sponsor used a prespecified testing sequence or another approach to control multiplicity.

For the primary efficacy outcome, the registry states that 804 patients with at least one postrandomization entry were included in the ITT Population and that an observed-cases approach was applied to missing postbaseline data. This identifies the stated population and missing-data approach, but does not explain the reasons for missing entries, their distribution between groups, or whether missingness was related to outcome. Those details are not reported in the registry record.

As a general statistical point, observed-case analyses use available outcome data and can be vulnerable to bias if the availability of measurements is related to response in ways not accounted for by the analysis. This is a limitation to consider, not evidence that bias occurred. The registry record does not report sensitivity analyses for missing primary outcome data, imputation procedures, or alternative assumptions about missing outcomes.

The original sample-size justification and full statistical analysis plan are also not reported in the registry record. Consequently, the planning illustrations based on observed effects cannot establish what assumptions guided enrollment, and the posted p-values cannot be linked to an undocumented multiplicity plan.

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: rotator cuff syndrome (0.2%), appendicitis (0.2%), cystopexy (0.2%), hodgkin's disease nodular sclerosis stage iva (0.2%), transient ischemic attack (0.2%).

The serious adverse event summaries report 7 affected participants among 403 at risk in the placebo group and 4 among 402 at risk in the linaclotide group. The registry also reports other, non-serious adverse events for 86 of 403 at risk in the placebo group and 137 of 402 at risk in the linaclotide group. These are counts of participants with reported events as presented in the registry, not a complete description of event duration, severity, recurrence, or causal attribution.

The listed serious adverse event terms each have a reported frequency of 0.2%: rotator cuff syndrome, appendicitis, cystopexy, Hodgkin's disease nodular sclerosis stage IVa, transient ischemic attack, and uterine leiomyoma. The registry record does not provide the number of participants associated with each listed term in this summary. Deaths are not reported in the registry record.

These figures should be read as descriptive safety counts, not as proof that an event was caused by treatment or that no other safety concerns occurred. Differences in counts alone do not establish a treatment-related risk difference, and the record does not provide confidence intervals or a detailed safety analysis for these comparisons.

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

The posted primary result shows that the observed proportion meeting the combined APC responder definition was higher in the linaclotide group than in the placebo group. The sponsor’s reported odds ratio and the unadjusted recalculations point in the same direction. The primary endpoint is specific: it asks whether a participant achieved repeated improvements in both complete spontaneous bowel movements and abdominal pain under the defined thresholds during the first 12 treatment weeks.

This finding does not mean every participant assigned to linaclotide met the responder definition. It also does not describe the size of symptom change among every participant, since a binary responder classification records whether the full rule was met rather than the degree of change for those who did not meet it. The separate secondary measures address other aspects of bowel and symptom response, but they are not interchangeable with the primary endpoint.

The result does not establish that the same effect would be observed in every population, over every duration, or under every clinical circumstance. The registry record describes a particular randomized trial in patients with IBS-C and an endpoint assessed to Week 12 within a 26-week study. Generalization beyond that population and setting requires evidence beyond this registry summary.

The result also does not, by itself, settle the balance of benefits and harms. The safety counts are descriptive, and the registry record does not provide enough detail to attribute individual adverse events to treatment or to evaluate every aspect of safety. Nor does a low p-value express the probability that the treatment effect is real or the probability that a particular person will respond.

Finally, important analytic details are not reported in the registry record, including the original sample-size justification, interim analysis plans, and multiplicity strategy. The primary result is interpretable as a randomized comparison for the reported endpoint, but those missing details constrain assessment of the complete statistical plan and the broader evidence.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters in clinical research. The primary measure is not simply a bowel movement count or an abdominal pain score; it requires both symptom domains to meet specified thresholds repeatedly. That joint definition can align the statistical outcome with a broader response concept, while also making the result dependent on the exact thresholds and time pattern chosen.

It also shows why effect measures should be distinguished. The sponsor reports an odds ratio, while the simple recalculation includes an absolute risk difference. Both describe a contrast between randomized groups, but they answer the comparison on different scales. Reporting the measure together with its confidence interval helps readers consider both direction and precision rather than relying only on whether a p-value crosses a threshold.

The trial’s record also demonstrates the importance of understanding analysis populations and missing-data handling. The primary analysis included patients with at least one postrandomization assessment entry and used observed cases for missing postbaseline data. Such details affect the population represented by the estimate and the assumptions required to interpret it.

Finally, a collection of secondary outcomes can enrich interpretation but also raises multiplicity questions. Directional consistency across related symptom measures can add context, yet unadjusted secondary tests should not automatically be treated as confirmatory. The missing reporting of the original design assumptions and multiplicity plan underscores why statistical results are strongest when estimates, uncertainty, endpoint definitions, populations, and analysis plans are all transparently reported.

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 primary endpoint combines multiple criteria into a responder classification. That can make the outcome straightforward to interpret as a participant count, but it hides the degree of change among people who did not meet every criterion and makes the conclusion dependent on the specified thresholds and repeated-response rule. The endpoint addresses the first 12 treatment weeks, whereas the trial is described as lasting 26 weeks; the primary finding should not be read as a summary of the full treatment period.

The primary efficacy analysis used observed cases for missing postbaseline data. The registry record does not report the reasons for missingness, group-specific missing-data patterns, sensitivity analyses, or the assumptions used to assess the impact of missing outcomes. The available summary therefore does not show how robust the estimate is to alternative missing-data assumptions.

The record does not report the original sample-size justification, the full statistical analysis plan, a multiplicity strategy, or whether interim analyses were planned. Those omissions limit assessment of how the primary analysis was prespecified and how the secondary tests were intended to be interpreted. The planning illustrations based on observed effects do not fill that gap.

The sponsor’s reported odds ratio and the unadjusted recalculation use different analytical approaches and effect measures. The summary does not report sufficient detail to reconstruct the sponsor’s method fully. The recalculated secondary standardized effects rely on approximate pooled variability derived from posted summary information, so they are not a replacement for a fully specified model-based analysis.

Safety summaries are counts without reported confidence intervals or detailed attribution. The registry record also does not report deaths in these safety data. As a result, the safety information in this summary is descriptive and does not support a comprehensive assessment of event causality or comparative risk.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial of Linaclotide in Patients With Irritable Bowel Syndrome With Constipation (IBS-C) — NCT00938717.
• Registry record last updated 2013-11-05; status last verified 2013-10.
• Results first posted 2013-01-30.
• 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

The registry describes a completed phase 3 randomized, double-blind, placebo-controlled, parallel-group trial of oral linaclotide in patients with IBS-C. The study enrolled 805 patients and compared linaclotide with matching placebo over 26 weeks. The primary outcome was the APC responder definition assessed from baseline to Week 12.

The sponsor-reported analysis found higher odds of meeting the primary responder definition in the linaclotide group than in the placebo group. The unadjusted recalculation is directionally consistent. The primary efficacy population included 804 patients with at least one postrandomization entry, and the registry states that observed cases were used for missing postbaseline data.

Secondary outcome summaries cover several bowel and symptom measures, while the safety record lists serious and other adverse event counts. The registry does not report the original sample-size justification, the full statistical plan, multiplicity handling, or a detailed account of missing-data patterns.