Trial of Linaclotide in Patients With Chronic Constipation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Linaclotide in Patients With Chronic Constipation (NCT00730015), a randomized phase 3 study. The primary outcome is Complete Spontaneous Bowel Movement (CSBM) Overall Responder.

2. Clinical Question

The trial asked whether patients with chronic constipation assigned to linaclotide were more likely than patients assigned to matching placebo to meet the protocol definition of a 12-week Complete Spontaneous Bowel Movement (CSBM) Overall Responder. The record describes two linaclotide dose groups, 145 μg and 290 μg, compared with placebo.

A responder had to meet both a frequency threshold and an increase-from-baseline threshold during at least 9 of the 12 treatment weeks. A CSBM was a spontaneous bowel movement accompanied by a sense of complete evacuation. For a bowel movement to count as spontaneous, the definition excluded bowel movements occurring on a calendar day when a laxative, enema, or suppository was used, and on the day after such use. Thus the endpoint combines bowel-movement frequency, change from baseline, treatment duration, and the patient’s sense of completeness. The question is not simply whether bowel movements occurred, but whether the specified pattern was sustained for much of the treatment period.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group trial. The registry lists quadruple masking, meaning the record identifies four masked parties but does not name them in the trial details. The trial evaluated oral linaclotide for 12 weeks, followed by a 4-week randomized withdrawal period. The record states that 643 patients were randomized and received at least 1 dose of study drug; 642 were included in the Intent to Treat population for the primary endpoint.

The primary outcome was assessed from baseline to Week 12. The three primary-outcome groups reported were linaclotide 145 μg, linaclotide 290 μg, and placebo. Their respective primary-outcome group sizes were 217, 216, and 209. These are the analysis denominators shown with the primary result and are not identical to the 643 randomized patients overall. The record says an observed-cases approach was used for missing postbaseline data. It does not provide a fuller account of how missing observations were handled at each visit or the reasons observations were missing.

The record identifies the trial as completed and gives the condition as chronic constipation. It describes the study objective as evaluating efficacy and safety. The randomized withdrawal period is part of the official trial description, and additional adverse-event groups are labeled according to treatment sequences during that period. The protocol details for that phase, including the criteria for entering it and its specific efficacy analyses, are not reported in the registry record. The original sample-size justification, the planned interim analyses, and the full statistical analysis plan are also not reported in the registry record. Those omissions limit what can be inferred about how the study was planned beyond the design features explicitly recorded.

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).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 643 randomized patients received at least 1 dose of study drug. 642 patients 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 Complete Spontaneous Bowel Movement (CSBM) Overall Responder, measured over Change from Baseline to Week 12.

The primary endpoint counts participants who met the trial’s definition of a CSBM Overall Responder by Week 12. A qualifying responder had a CSBM weekly frequency rate of 3 or greater and an increase of 1 or more from baseline in at least 9 of the 12 treatment weeks. The definition therefore requires both a specified weekly frequency and improvement relative to the participant’s own baseline, with the criteria met across most of the treatment period.

A CSBM is a spontaneous bowel movement associated with a sense of complete evacuation. The trial defines a spontaneous bowel movement as one occurring without laxative, enema, or suppository use on that day or the previous calendar day. This distinction is intended to separate bowel movements occurring without those rescue measures from those associated with their use. The endpoint is binary for each participant: the participant either meets the responder definition or does not.

Such a responder endpoint can be useful because it expresses the outcome as the number of participants meeting a predefined composite threshold, rather than only as an average change. It also has limitations: the result depends on the chosen thresholds, the duration requirement, and the baseline comparison. A participant just short of one criterion is classified differently from one who meets all criteria, even if their underlying bowel-movement patterns are similar. The registry record gives the endpoint definition and its timeframe, but does not report the rationale for choosing these particular thresholds.

7. Results Posted in the Registry

• Linaclotide, 145μg: 21.2% (46/217) versus 3.3% (7/209) on control; risk difference 17.8 percentage points (95% CI 11.9 to 23.8), risk ratio 6.33 (2.92–13.70); unadjusted two-proportion z-test p = <0.001.
• Linaclotide, 290μg: 19.4% (42/216) versus 3.3% (7/209) on control; risk difference 16.1 percentage points (95% CI 10.3 to 21.9), risk ratio 5.81 (2.67–12.63); 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, 145μg: mean 1.94 versus 0.45 on control; difference 1.49 (95% CI 1.02 to 1.96), standardized effect d = 0.60; z-test p = <0.001.
  • Linaclotide, 290μg: mean 2.04 versus 0.45 on control; difference 1.59 (95% CI 1.12 to 2.06), 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, 145μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide, 290μg 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, 145μg: mean 3.03 versus 1.08 on control; difference 1.95 (95% CI 1.35 to 2.55), standardized effect d = 0.62; z-test p = <0.001.
  • Linaclotide, 290μg: mean 2.98 versus 1.08 on control; difference 1.90 (95% CI 1.30 to 2.50), standardized effect d = 0.61; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide, 145μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide, 290μg 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, 145μg: mean 1.85 versus 0.58 on control; difference 1.27 (95% CI 1.03 to 1.51), standardized effect d = 1.11; z-test p = <0.001.
  • Linaclotide, 290μg: mean 1.84 versus 0.58 on control; difference 1.26 (95% CI 1.02 to 1.50), standardized effect d = 1.11; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide, 145μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Linaclotide, 290μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry names secondary outcomes covering CSBM frequency, SBM frequency, stool consistency, straining, abdominal discomfort, bloating, and constipation severity. Numerical group comparisons are available in the posted results for CSBM frequency, SBM frequency, and stool consistency. For these outcomes, the reported mean changes are greater in both linaclotide groups than in the placebo group, and the simple unadjusted comparisons have p-values of <0.001. This broad direction is consistent with the primary responder result: the primary endpoint counts participants meeting a sustained CSBM threshold, while the secondary measures describe average changes in related dimensions.

The secondary outcomes add context, but they are not equivalent to the primary endpoint. A group-average change does not reveal how many individuals met the responder definition, and the binary responder outcome does not show the full distribution of changes. Agreement in direction across measures can make the overall pattern easier to describe, but it does not independently validate the endpoint or eliminate uncertainty about missing data and analysis details.

Unadjusted secondary p-values carry less weight when several outcomes are examined because repeated testing increases the chance of at least one apparently strong result arising by chance. In general, multiplicity procedures can control that risk, but the registry record does not report whether or how multiplicity was addressed for secondary outcomes. The secondary p-values should therefore be viewed as descriptive evidence rather than as a set of independently confirmatory tests.

Although the record lists additional secondary outcomes for straining, abdominal discomfort, bloating, and constipation severity, numerical comparisons for those outcomes are not reported in the registry record. Their direction, magnitude, and precision should not be inferred from the outcomes with posted results. The available secondary results support a consistent pattern across the three measures with numerical data, but they cannot establish the pattern for every outcome named in the trial record.

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 Discomfort
• 12-week Change in Bloating
• 12-week Change in Constipation Severity

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as a responder or nonresponder. In general, a binary endpoint can be summarized by counting participants with the event in each group and relating those counts to the group sizes. The primary record reports 46 responders among 217 participants for 145 μg, 42 among 216 for 290 μg, and 7 among 209 for placebo. The comparison estimates quantify differences between each linaclotide group and placebo. Because both active groups are compared with the same placebo group, the two comparisons are related through their shared comparator; they are not two wholly independent experiments.

What does a risk difference express?

In general, a risk difference subtracts the event probability in one group from the event probability in another. It is an absolute measure: it describes the gap between group probabilities on the original probability scale. The recalculated values are 0.178 for 145 μg versus placebo and 0.161 for 290 μg versus placebo. These are unadjusted recalculations from the posted event counts and group sizes. Their confidence intervals are 0.119 to 0.238 and 0.103 to 0.219, respectively. A risk difference is distinct from a risk ratio or odds ratio, which compare relative quantities rather than the absolute gap.

What does the sponsor’s odds-ratio analysis express?

The registry’s own analysis reports odds ratios using the Cochran-Mantel-Haenszel method. In general, an odds ratio compares the odds of the event in one group with the odds in another. It is not an absolute probability difference, and an odds ratio should not be interpreted as a multiplicative change in probability. The reported odds ratios are 7.72 for 145 μg versus placebo and 7.21 for 290 μg versus placebo. Their 95% confidence intervals and p-values are reported with the sponsor’s analyses. The registry identifies the method but does not report the strata or other implementation details, so those should not be inferred.

The recalculated p-values are unadjusted and are based on a simple comparison of the posted summary data. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The sponsor-reported analyses use a different effect measure and method; the sponsor’s own analysis takes precedence when describing the sponsor’s analysis. The record does not report a multiplicity procedure for the primary comparisons.

How are the continuous secondary outcomes summarized?

The posted secondary results include least-squares means for change from baseline to Week 12. A least-squares mean is a model-based group mean; the registry record does not give enough model detail to reconstruct the adjustment or specification behind these reported means. The comparisons in the recalculation use mean differences between the linaclotide group and placebo. For example, the posted CSBM-frequency mean differences are 1.49 for 145 μg and 1.59 for 290 μg. The recalculated 95% confidence intervals are 1.019 to 1.961 and 1.119 to 2.061.

For these continuous outcomes, the displayed spread is a standard error. In general, a standard error describes the uncertainty in an estimated mean, rather than the spread of individual participant observations. The recalculated pooled standard deviations are marked as approximate because they were inferred using the reported standard errors and group sizes. They are not directly reported standard deviations from participant-level data. A mean difference describes a contrast in group averages; it does not imply that every participant experienced that change.

Why can over-dispersion matter for counts?

In general, count outcomes may vary more between participants than a simple count model assumes. This is called over-dispersion. If it is present and not handled appropriately, standard errors and confidence intervals from a model that assumes less variation can be too small, making the results appear more precise than warranted. The registry’s numerical summaries do not report a model for participant-level count data or a dispersion assessment, so no conclusion about over-dispersion can be drawn from these summary values alone.

The sample-size illustrations use the observed effects as planning inputs, with smaller fractions of those effects also considered. They are generic calculations under the listed assumptions, not a reconstruction of the trial’s original design. In general, a sample-size calculation depends on a target effect, a significance threshold, allocation, outcome variability, and a desired probability of detecting the target effect when it is present. The registry record does not report the trial’s original sample-size justification, the assumptions used in its design, or whether interim analyses were planned.

The analyses available in the registry are based on group-level summaries. Without participant-level data, the recalculations cannot test alternative endpoint definitions, fit different covariate models, assess patterns of missingness, or verify all details of the sponsor’s procedure. The distinction between registry-reported analyses and simple recalculations is therefore important: the latter help interpret the posted summaries but do not replace the study’s full statistical analysis.

11. Confidence Intervals and Precision

Confidence intervals describe uncertainty around an estimated effect under the assumptions of the analysis. For the primary outcome, the recalculated risk-difference interval for 145 μg versus placebo is 0.119 to 0.238; for 290 μg versus placebo it is 0.103 to 0.219. Both intervals lie above zero, which is consistent with the observed direction of the comparisons. The intervals are not guarantees that the true effect lies within those exact limits, and they do not include uncertainty from aspects that the simple recalculation does not model.

The width of a confidence interval reflects both the amount of information and the variability relevant to the estimate. In general, more observations can improve precision, while sparse events can leave estimates less precise. The placebo group had 7 primary responders among 209 participants, while the two linaclotide groups had 46 of 217 and 42 of 216. The reported odds-ratio intervals are notably broad in absolute terms: 3.41 to 17.47 for the 145 μg comparison and 3.14 to 16.59 for the 290 μg comparison. They nevertheless exclude an odds ratio of 1. These odds-ratio intervals and the risk-difference intervals describe different scales and should not be compared as if they were interchangeable.

The continuous secondary comparisons also have confidence intervals. For CSBM frequency, the mean-difference intervals are 1.019 to 1.961 and 1.119 to 2.061. For SBM frequency, they are 1.354 to 2.546 and 1.304 to 2.496. For stool consistency, they are 1.034 to 1.506 and 1.024 to 1.496. These intervals reflect uncertainty in estimated differences in group means, not individual-level ranges. Their precision depends on the reported model-based means and standard errors; the registry record does not provide the complete modeling details needed to independently verify those intervals.

Precision is not the same as importance. A narrow interval can indicate a more precisely estimated effect without establishing whether that effect is meaningful in practice. Conversely, a statistically clear estimate does not remove uncertainty about the endpoint’s thresholds, missing data, generalizability, or unreported analysis details.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For these binary and continuous comparisons, the figures are participants per arm, not total participants across both arms and not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to provide an 80% probability of detecting the specified effect under those planning assumptions, if that effect is present and the assumptions hold. The 90% power column gives the corresponding estimate for a 90% probability. These are planning probabilities conditional on the assumptions, not guarantees about the results of a future study. The figures are not observed power.

Rows that plan for 100% of the observed effect use the full effect estimated in this trial as the target. Rows for 75% and 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so they generally require more participants per arm to reach the same planned power. For example, the primary comparison for 145 μg lists 52 participants per arm for 80% power when planning for 100% of the observed effect, compared with 78 when planning for 75% and 141 when planning for 50%. These figures are illustrative and inherit uncertainty from the observed effect used as their starting point.

The assumptions do not establish that the original investigators used the same target effects or methods. The registry record does not report the original sample-size calculation, the design effect assumed for planning, or a rationale for selecting a particular power target. The illustrations should therefore be read as conditional examples of how sample size changes with the target effect, rather than as evidence about the trial’s design quality or achieved power.

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 = 0.033; treatment proportion p₁ = 0.212; average p̄ = 0.123.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4641 = 0.9095.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4466 = 0.3758.
4. n = (0.9095 + 0.3758)² / (0.1785)² = 51.9, rounded up to 52 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 <- 0.0334928229665072                          # control proportion
p1 <- 0.211981566820276                          # 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(730015)
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 = 52 (80% power), 69 (90% power)
 75% of observed effect: n per arm = 78 (80% power), 104 (90% power)
 50% of observed effect: n per arm = 141 (80% power), 188 (90% power)
power.prop.test: 51.9 
Simulated power at n = 52 per arm: 0.844 (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 registry reports the sponsor’s primary comparisons as Cochran-Mantel-Haenszel odds ratios. For 145 μg versus placebo, the reported odds ratio is 7.72, with a 95% confidence interval from 3.41 to 17.47 and p < 0.001. For 290 μg versus placebo, the reported odds ratio is 7.21, with a 95% confidence interval from 3.14 to 16.59 and p < 0.001. These are the sponsor’s own reported analyses and should be used when describing its analysis.

The simple recalculations instead report unadjusted risk differences from the posted event counts and denominators. They are 0.178 for 145 μg versus placebo and 0.161 for 290 μg versus placebo, with corresponding 95% confidence intervals of 0.119 to 0.238 and 0.103 to 0.219. The recalculations also report odds ratios, but they do not reproduce the sponsor’s stated odds-ratio values exactly. The quantities arise from different analysis procedures and, in the recalculation, a simple unadjusted comparison. The registry record does not provide enough detail to identify every reason for the numerical differences.

The record does not flag a discrepancy between the posted results and the sponsor analysis. The sponsor’s reported results take precedence for describing the sponsor’s statistical analysis; the recalculated risk differences are supplementary ways to express the posted group counts. The two effect measures answer related but distinct questions, so their numerical magnitudes should not be compared directly.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses or outcomes are tested. Even if each test uses the same nominal significance threshold, the chance of at least one small p-value across a family of tests can increase as the number of tests grows. This matters in a trial with two dose comparisons against placebo and several secondary outcomes. The registry record reports the primary comparisons and several secondary results, but a multiplicity adjustment strategy is not reported in the registry record. It is therefore not possible to determine from the record whether the reported p-values were intended as confirmatory across a defined family of tests or whether any adjustment was used.

The primary endpoint analysis population is described as 642 participants in the Intent to Treat population. The record also says 643 randomized patients received at least 1 dose of study drug. For the endpoint, an observed-cases approach was applied to missing postbaseline data. In general, an observed-cases approach uses available observations rather than filling in missing outcomes with an assumed value. Its interpretation depends on why data are missing and whether missingness is related to outcomes or treatment. The record does not report the amount, timing, or reasons for missing data, nor does it provide sensitivity analyses under alternative missing-data assumptions.

The stated endpoint uses repeated weekly criteria over the treatment period. Missing postbaseline observations may therefore affect whether a participant can be classified as meeting the responder definition, but the registry record does not explain the detailed classification rules for incomplete weekly data. That missing detail limits independent assessment of how missing observations may have influenced the primary result.

The record identifies the sponsor’s Cochran-Mantel-Haenszel method for its odds-ratio analyses, but the strata and other implementation details are not reported in the registry record. The original sample-size justification, planned interim analyses, and complete statistical analysis plan are also not reported in the registry record. These omissions do not negate the reported estimates, but they limit the ability to reconstruct the full prespecified analysis strategy or assess whether all planned analyses are represented.

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: atrial fibrillation (1.1%), pulmonary embolism (1.1%), gastroenteritis viral (0.5%), pneumonia (0.5%), parathyroid tumor benign (0.5%).

The registry reports serious adverse events and a separate count for other adverse events in the initial treatment groups. Serious adverse events were reported for 3 of 217 participants in the 145 μg group, 4 of 217 in the 290 μg group, and 5 of 209 in the placebo group. The other adverse-event counts were 27 of 217, 30 of 217, and 14 of 209, respectively. These counts should be read as registry-reported group totals, not as estimates of causation or as a complete description of the nature, timing, or severity of every event.

The record also lists serious adverse-event terms with percentages: atrial fibrillation and pulmonary embolism at 1.1% each, and viral gastroenteritis, pneumonia, benign parathyroid tumor, and bronchitis at 0.5% each. The record does not provide enough detail in these summaries to connect each listed term to a particular treatment group or to assess event timing and exposure duration. The withdrawal-period groups have separate denominators and treatment-sequence labels; their counts should not be combined casually with the initial parallel-group counts. Deaths are not reported in the registry record.

These figures are descriptive. Differences in event counts alone do not establish that a treatment caused or prevented an event, and the registry summaries do not provide the detailed clinical context needed for individual safety judgments.

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

The posted primary results show that more participants in each linaclotide group met the defined CSBM Overall Responder threshold than in the placebo group during the 12-week assessment. The reported sponsor analyses and the simple unadjusted recalculations both show a strong statistical separation in the same direction. The result applies to this specific endpoint definition, these randomized groups, and the available observations analyzed as described in the registry record.

The outcome does not describe every aspect of chronic constipation or every participant’s experience. It is a binary classification based on a frequency threshold, an increase from baseline, and success in at least 9 of the 12 treatment weeks. Participants who did not meet every criterion are counted as nonresponders, even though their individual patterns may have varied. The endpoint also incorporates a sense of complete evacuation and excludes bowel movements around use of specified rescue measures. The record does not report the rationale for all of these design choices.

The reported comparisons do not establish what would happen outside the trial population, over a different treatment duration, or under a different outcome definition. The registry record does not provide enough information to evaluate all aspects of generalizability, including the participant characteristics needed to compare the study population with other settings. The available numerical results also do not establish effects on every secondary outcome named in the record, because numerical comparisons for some of those outcomes are not reported in the registry record.

Statistical significance is not a measure of practical importance, and neither a p-value nor a confidence interval answers every clinical question. This statistical account describes the posted results and their precision; it is not medical advice and does not make a treatment recommendation. Interpretation should consider the outcome definition, the unadjusted nature of recalculations, the reported missing-data approach, multiplicity information, and the limits of registry-level detail.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical outcome can be defined as a participant-level responder criterion rather than only as an average change. The CSBM Overall Responder definition requires a specified weekly frequency, an increase from baseline, and repeated success over much of the 12-week treatment period. That structure makes the estimand understandable as a count of participants meeting a prespecified pattern, while also making the result dependent on the threshold choices.

It also shows why effect measures should be distinguished. The simple recalculations express the primary contrast as a risk difference, an absolute gap in responder probability, whereas the registry’s own analysis reports odds ratios. Both can describe the same two-group comparison, but they use different scales and are not interchangeable. Reporting the event counts alongside the effect estimates helps readers connect the statistical summary to the observed groups.

The case also highlights the importance of uncertainty and analysis provenance. The risk-difference confidence intervals are distinct from the sponsor-reported odds-ratio intervals, and the sponsor analysis uses a named Cochran-Mantel-Haenszel method. A simple recalculation can provide a transparent companion view of summary data, but it cannot recreate unreported model details, missing-data decisions, or planned multiplicity procedures. Keeping sponsor-reported analyses separate from unadjusted recalculations prevents a derived estimate from being mistaken for the study’s own analysis.

Finally, the trial record links a primary endpoint to several secondary measures and a randomized withdrawal period. That combination makes careful separation of endpoint families, analysis populations, and treatment phases important. The record’s missing details about design assumptions and multiplicity are not merely technical gaps: they shape how confidently readers can reconstruct the original analysis plan and how much weight to place on multiple reported comparisons.

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 original sample-size justification, so the planning rationale cannot be assessed from the posted record. The sample-size illustrations use observed effects and stated generic assumptions; they do not establish what effect the trial was designed to detect. The record also does not report whether interim analyses were planned or provide the complete statistical analysis plan.

The primary endpoint uses a demanding composite threshold over repeated weeks. The posted responder counts do not show the distribution of weekly CSBM frequency, the amount of change among nonresponders, or how participants close to a threshold differed from those meeting it. The registry record gives the endpoint definition but not the rationale for its thresholds. It also does not provide detailed rules for classifying participants with incomplete weekly data.

Missing postbaseline data were handled using an observed-cases approach, but the record does not state how much data were missing, when they were missing, or why. No alternative missing-data sensitivity analyses are reported in the registry record. These omissions make it difficult to assess how robust the responder classification is to different assumptions about missing observations.

The registry reports sponsor odds ratios using a Cochran-Mantel-Haenszel method but does not provide the strata or full analysis specification. The simple risk-difference and continuous-outcome recalculations are unadjusted and depend on posted summary statistics. For the continuous secondary outcomes, pooled standard deviations in the recalculations are approximate, inferred from reported standard errors and group sizes rather than posted as direct participant-level estimates.

Multiplicity handling is not reported in the registry record, and numerical results are not reported for every secondary outcome named. Safety summaries provide counts and selected serious-event terms but not enough detail to assess timing, exposure-adjusted rates, or causal attribution. Finally, the trial record alone does not provide all participant characteristics or contextual details needed to judge how broadly the results may apply.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial of Linaclotide in Patients With Chronic Constipation — NCT00730015.
• Registry record last updated 2013-01-30; status last verified 2012-12.
• 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

NCT00730015 is a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group trial of linaclotide in patients with chronic constipation. The study evaluated 145 μg and 290 μg linaclotide against matching placebo, with a 12-week treatment period followed by a 4-week randomized withdrawal period. The primary endpoint was the 12-week CSBM Overall Responder definition, which required a specified CSBM frequency and increase from baseline in at least 9 of 12 weeks.

The primary counts were 46 of 217 for 145 μg, 42 of 216 for 290 μg, and 7 of 209 for placebo. The sponsor reported odds ratios of 7.72 and 7.21 for the two comparisons, each with p < 0.001. The record describes an observed-cases approach for missing postbaseline data. It does not report the original sample-size justification, multiplicity strategy, interim-analysis plan, or full statistical analysis plan.