TELESTAR (Telotristat Etiprate for Somatostatin Analogue Not Adequately Controlled Carcinoid Syndrome): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TELESTAR (Telotristat Etiprate for Somatostatin Analogue Not Adequately Controlled Carcinoid Syndrome) (NCT01677910), a randomized phase 3 study. The primary outcome is Change From Baseline in the Number of Bowel Movements (BMs) Per Day Averaged Over 12 Weeks.

2. Clinical Question

3. Trial Design

TELESTAR (NCT01677910) was a Phase 3, randomized, placebo-controlled, parallel-group, multicenter, double-blind study sponsored by Lexicon Pharmaceuticals. The registry lists quadruple masking. The study was completed; its recorded start date was 2013-01-08 and its primary completion date was 2016-03-21. Enrollment was 135.

The double-blind treatment period followed a 3 to 4-week run-in on stable-dose SSA therapy. The treatment groups were placebo, 250 mg telotristat etiprate, and 500 mg telotristat etiprate, each administered three times daily during the 12-week treatment period. The placebo arm description also refers to a 36 week open-label extension. Participants assigned to active treatment were described as entering an open-label extension as well. The extension was not part of the primary 12-week endpoint.

The primary outcome was change from baseline in daily bowel movements averaged over 12 weeks. The registry describes daily diary recording and analysis of the average. Results are reported for 45 participants in each double-blind group. The stated primary analysis population was the intent-to-treat population, all randomized participants with data available; further detail about missing outcome data and analysis handling is not reported in the registry record.

Three secondary outcomes are posted: urinary 5-hydroxyindoleacetic acid (u5-HIAA), daily cutaneous flushing episodes, and abdominal pain. The registry record reports serious and other adverse-event counts for the double-blind groups and an open-label extension group. Randomization and masking are features intended to limit systematic differences and bias, but details of the allocation procedure, masking procedures, and conduct are not reported in the registry record.

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 with Carcinoid Syndrome not adequately controlled by somatostatin analog (SSA) therapy were assigned in a 1:1:1 ratio to receive placebo, 250 mg or 500 mg telotristat etiprate (LX1606) in the double-blind period and were eligible to receive 500 mg telotristat etiprate in the 36 week open-label extension. 136 randomized;1 patient twice.

Double-Blind Treatment Period

Reasons for not completing this period:

Open-Label Extension Period (OLE)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants from the Intent-to-treat population, all randomized participants, with data available were included in the analyses.

5. Baseline Characteristics

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

Population: Safety population

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Number of Bowel Movements (BMs) Per Day Averaged Over 12 Weeks, measured over Baseline and 12 Weeks.

The primary endpoint is change from baseline in the number of bowel movements per day, averaged over the 12-week double-blind treatment period. Participants recorded bowel movements in a daily diary, and the daily counts were averaged across the period. The unit is counts per day. A negative change means that the average count during treatment was lower than the baseline value.

This endpoint directly measures the symptom named in the registry’s primary objective. Using a daily diary captures repeated reports over the treatment period rather than relying only on a single report at its end. Averaging the records gives a continuous outcome that can be summarized by a group mean and standard deviation, as the posted results do. It also means the group result reflects the recorded values available for analysis; the registry does not report the completeness of diary entries or how missing diary data were handled.

The endpoint is change from baseline, not the absolute number of bowel movements during treatment. A comparison of changes between groups therefore asks whether the average shift from baseline differs between a telotristat etiprate group and placebo. The primary result should be read in that context, with the units and uncertainty in mind. The endpoint alone does not describe every aspect of carcinoid syndrome, and the registry does not report a threshold for a change that participants would consider important.

7. Results Posted in the Registry

• 250 mg Telotristat Etiprate: mean -1.43 versus -0.62 on control; difference -0.81 (95% CI -1.28 to -0.34), standardized effect d = -0.72; z-test p = <0.001.
• 500 mg Telotristat Etiprate: mean -1.46 versus -0.62 on control; difference -0.83 (95% CI -1.28 to -0.38), standardized effect d = -0.76; 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.

Change From Baseline in Urinary 5-hydroxyindoleacetic Acid (u5-HIAA) Levels

• 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 deviations.
• Result:
  • 250 mg Telotristat Etiprate: mean -40.13 versus 11.35 on control; difference -51.48 (95% CI -83.42 to -19.55), standardized effect d = -0.78; z-test p = 0.002.
  • 500 mg Telotristat Etiprate: mean -57.52 versus 11.35 on control; difference -68.87 (95% CI -100.45 to -37.29), standardized effect d = -1.08; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for 250 mg Telotristat Etiprate 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 lower for 500 mg Telotristat Etiprate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Number of Daily Cutaneous Flushing Episodes Averaged Across All Time-Points

• 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 deviations.
• Result:
  • 250 mg Telotristat Etiprate: mean -0.30 versus -0.16 on control; difference -0.13 (95% CI -0.64 to 0.38), standardized effect d = -0.11; z-test p = 0.612.
  • 500 mg Telotristat Etiprate: mean -0.53 versus -0.16 on control; difference -0.36 (95% CI -0.88 to 0.16), standardized effect d = -0.29; z-test p = 0.172.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 250 mg Telotristat Etiprate and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 500 mg Telotristat Etiprate and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Abdominal Pain Averaged Across All Time-Points

• 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 deviations.
• Result:
  • 250 mg Telotristat Etiprate: mean -0.49 versus -0.23 on control; difference -0.26 (95% CI -0.80 to 0.28), standardized effect d = -0.20; z-test p = 0.341.
  • 500 mg Telotristat Etiprate: mean -0.33 versus -0.23 on control; difference -0.11 (95% CI -0.59 to 0.38), standardized effect d = -0.09; z-test p = 0.664.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 250 mg Telotristat Etiprate and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 500 mg Telotristat Etiprate and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide additional measures related to carcinoid syndrome: urinary u5-HIAA, daily cutaneous flushing episodes, and abdominal pain. In broad terms, the posted u5-HIAA group results and unadjusted comparisons show reductions relative to placebo, whereas the flushing and abdominal pain comparisons are less clearly separated from placebo in the unadjusted analyses. This pattern is not as consistent across outcomes as the primary bowel-movement result.

These outcomes add context, but they are not interchangeable with the primary endpoint. They measure different features, use different units or scales, and can have different amounts of variability and available data. The u5-HIAA analyses use fewer participants with reported values than the primary endpoint. The registry does not report the reasons for these differences in available data. Secondary results should therefore be considered alongside their own uncertainty and the completeness of the underlying observations.

The registry does not post sponsor-reported inferential analyses for the secondary outcomes. The available contrasts are unadjusted re-calculations from summary statistics. In general, when several outcomes or comparisons are examined, the chance of seeing an apparently notable result by chance can increase. Multiplicity methods can address that issue, but the adjustment procedure for this trial is not reported in the registry record.

Accordingly, the secondary findings are supporting context rather than independent confirmation of the primary result. Their overall pattern can suggest which other measured outcomes moved in a similar or different direction, but the registry information does not establish a formal hierarchy, confirmatory status, or multiplicity strategy. Those details are not reported in the registry record.

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

• Change From Baseline in Urinary 5-hydroxyindoleacetic Acid (u5-HIAA) Levels
• Change From Baseline in the Number of Daily Cutaneous Flushing Episodes Averaged Across All Time-Points
• Change From Baseline in Abdominal Pain Averaged Across All Time-Points

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change in bowel movement counts per day. The registry gives group sample sizes, means, and standard deviations. A standard deviation describes how spread out participant-level values are around a group mean. It is not the same as a confidence interval, which expresses uncertainty around an estimated quantity. Greater variability can make a group mean less precise, even when the mean itself is unchanged.

What is the reported comparison?

The registry reports two Wilcoxon rank sum comparisons, each contrasting an active-treatment group with placebo. The reported parameter is called “Mean Difference (Net),” and each comparison is identified as a superiority analysis. A rank-sum test works with the ordering of observations rather than relying solely on a normal-distribution model for the original measurements. The record does not provide enough detail to establish how the reported net mean difference and its confidence interval were calculated alongside the rank-sum test, so those details are not inferred.

The numerical re-calculations are unadjusted contrasts of posted summary statistics. They compare the group means and use the posted standard deviations and group sizes to estimate a mean difference and its confidence interval. They are not a reconstruction of the sponsor’s participant-level analysis and do not account for any adjustment or model that is not described in the registry record. Because the discrepancy indicator is false, the recalculated estimates are broadly consistent with the sponsor-reported estimates; the sponsor’s reported analysis remains the trial’s own inferential result.

How should a confidence interval be read?

A confidence interval gives an interval estimate rather than a single point estimate. In general, it communicates the precision of the estimate under the method used: a narrower interval indicates less statistical uncertainty, while a wider interval indicates more. Its endpoints should be interpreted with the direction and units of the outcome. For the primary outcome, the contrast is in counts per day, and zero represents no difference in average change between the compared groups. An interval that includes zero is compatible with no group difference under that interval procedure; an interval entirely on one side indicates a contrast in that direction, while still leaving uncertainty about its precise size.

A confidence interval is not a range containing every individual response, and it does not guarantee that a future study will reproduce the observed estimate. It also does not determine clinical importance. No clinical-importance threshold for the primary endpoint is reported in the registry record.

Why can over-dispersion matter?

In general, over-dispersion occurs when the observed variability in data is greater than a model assumes. If a model underestimates variability, its standard errors may be too small and its confidence intervals too narrow. Bowel movement counts are count data, but the registry reports a mean and standard deviation for the averaged outcome and reports a rank-sum method for the sponsor’s primary comparisons. It does not report an over-dispersion assessment or a count-regression model. The available information therefore does not support claiming that over-dispersion was tested or that a particular model addressed it.

What does the p-value say?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The sponsor reports p < 0.001 for both primary comparisons. The recalculated p-values are also unadjusted. The registry record does not report whether the sponsor’s p-values account for multiple comparisons or other features of the design.

What can the secondary analyses establish?

The secondary results are posted as group means and standard deviations with unadjusted recalculated contrasts. The registry does not list sponsor-reported inferential analyses for these outcomes. Multiple outcomes and comparisons increase the chance that at least one result may appear persuasive by chance if each is considered without accounting for the full set. In general, multiplicity procedures can control that risk, but the procedure used for this trial is not reported in the registry record. The secondary results are consequently best read as additional descriptive and exploratory evidence, not as a substitute for the primary analysis.

All these methods depend on the data available and the analysis assumptions. The registry states that the primary analysis included intent-to-treat participants with data available, but does not report missing-data methods, outcome imputation, sensitivity analyses, or a fuller statistical analysis plan. Those unknowns limit independent evaluation of how robust the estimates are to incomplete records or alternative analysis choices.

11. Confidence Intervals and Precision

The primary comparisons have sponsor-reported 95% confidence intervals of -1.283 to -0.337 counts/day for 250 mg telotristat etiprate versus placebo and -1.292 to -0.374 counts/day for 500 mg versus placebo. Both intervals lie below zero, consistent with the reported negative mean differences. The intervals also show that the estimate is not a single fixed value: a range of magnitudes remains compatible with the analysis.

In general, a confidence interval’s width reflects statistical precision under the method used. Precision depends on factors such as variability, the amount of information available, and the analysis method. The posted primary group standard deviations differ, and the registry does not give individual-level data or full model details to investigate their influence further. The reported intervals should therefore be interpreted as the sponsor’s estimates under its analysis, not as independently verified intervals from raw data.

The intervals do not describe the range of participant outcomes, nor do they show whether the average change is large enough to matter to participants. No threshold for a clinically important difference is reported in the registry record. A narrow or statistically separated interval cannot by itself answer that clinical question. Similarly, intervals for secondary outcomes that include zero indicate uncertainty about the direction of the group contrast; they do not establish that the groups are identical.

The confidence level is a property of the interval procedure under its assumptions, not a guarantee about this particular interval. The registry does not report additional sensitivity analyses or a full explanation of interval construction. The strongest reading is therefore that the posted primary estimates favor a greater average reduction in daily bowel movements relative to placebo, with the stated uncertainty, while the exact precision and robustness cannot be independently assessed from the registry record alone.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are participants per arm for comparisons between two groups; they are not totals across the trial. They use 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 trial’s original design assumptions are not reported in the registry record, so these illustrations should not be read as the sample-size plan used to design TELESTAR.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the chosen effect under those planning assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm. These are planning concepts, not guarantees about a future result.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. A smaller difference is harder to distinguish from variability, so more information is generally needed to achieve the same target power. The estimates are sensitive to the observed effect used as their starting point; an effect estimated from a completed trial may not be the effect that would occur in a new study. These figures are planning illustrations, not observed power.

For the primary comparisons, the planning inputs are based on the recalculated unadjusted effects and pooled variability. They do not incorporate a multiplicity adjustment, missing-data allowance, or other design features unless stated in the planning assumptions. They should be treated as an illustration of how assumed effect size relates to participant requirements, rather than a recommendation or a reconstruction of the trial’s original design.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.810; pooled standard deviation σ = 1.129.
2. n = 2 × (1.96 + 0.842)² × 1.129² / -0.810² = 30.5, rounded up to 31 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.81                      # observed difference in means
sigma <- 1.12883286849737                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1677910)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 31 (80% power), 41 (90% power)
 75% of observed effect: n per arm = 55 (80% power), 73 (90% power)
 50% of observed effect: n per arm = 122 (80% power), 164 (90% power)
power.t.test: 31.5 
Simulated power at n = 31 per arm: 0.795 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analyses use the Wilcoxon rank sum method and report a mean difference (net) for each active-treatment comparison with placebo. The sponsor-reported estimate is -0.81 for 250 mg telotristat etiprate and -0.833 for 500 mg telotristat etiprate. Each reported 95% confidence interval is below zero, and each p-value is < 0.001.

The recalculated estimates are simple, unadjusted comparisons of the posted group means and standard deviations. They yield -0.81 for 250 mg and -0.832 for 500 mg. These calculations are useful as a check on the broad direction and scale of the posted group summaries, but they do not reproduce the sponsor’s participant-level rank-sum analysis. Small differences in estimates or interval endpoints can arise because the methods and available information differ.

The registry marks no discrepancy between the recalculated and reported analyses. The sponsor’s analysis is the trial’s own reported inferential analysis; the recalculation is supplementary and should not replace it. The registry does not report enough detail to independently reproduce the sponsor’s method or determine all adjustments, if any, used in its analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and several secondary outcomes, with comparisons of each active-treatment group against placebo. Examining several outcomes and contrasts creates a multiplicity issue: even when no true difference exists for a particular comparison, the chance of at least one apparently unusual result can rise across a family of tests. In general, statistical plans may control this through a prespecified hierarchy, adjusted significance levels, or other methods.

A multiplicity adjustment or testing hierarchy is not reported in the registry record. The primary analyses have sponsor-reported p-values, while secondary outcomes have unadjusted recalculated comparisons and no sponsor-reported inferential analyses. Without a reported strategy, the secondary p-values should not be interpreted as if they had been protected against the full set of outcomes and comparisons. The record also does not describe interim analyses or stopping rules; those details are not reported in the registry record.

The primary analysis population is described as intent-to-treat, including all randomized participants with data available. This identifies the intended population but does not explain how participants without outcome data were handled, why data may be unavailable, or whether any imputation or sensitivity analysis was used. These missing-data methods are not reported in the registry record. If the availability of outcome data is related to treatment or outcome, an analysis restricted to those with data may not fully represent all randomized participants.

The registry does not provide a complete statistical analysis plan, details of randomization implementation, or a full account of model covariates and assumptions. It also does not report whether the primary analysis used any adjustments beyond the identified rank-sum method. These omissions do not erase the posted estimates, but they limit assessment of prespecification, analytic robustness, and the possibility of selective emphasis. Conclusions should therefore distinguish the sponsor’s reported primary analysis from exploratory or unadjusted secondary calculations.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: investigation (4.4%), abdominal pain (4.3%), radiotherapy (2.6%), general physical health deterioration (2.6%), desseminated intravascular coagulation (2.2%).

The registry reports serious adverse-event counts for the double-blind groups and the open-label extension group. Serious events affected 7 participants in the placebo group, 7 in the 250 mg group, and 8 in the 500 mg group. The extension group lists 37 participants affected. The corresponding groups at risk are 45, 45, 45, and 115. The extension was open-label and should be read separately from the randomized double-blind comparisons.

Other adverse-event counts are 39 for placebo, 37 for 250 mg, 42 for 500 mg, and 110 for the extension group. Deaths are listed as 3, 1, 1, and 9, respectively. These are registry counts, not estimates of comparative risk, and the group sizes and observation context differ for the extension. The record does not provide enough detail to establish timing, attribution, event overlap, or causal relationship to treatment.

The registry also lists serious-event terms and percentages, including Investigation at 4.4% and Abdominal Pain at 4.3%. Such listings describe reported events; they do not by themselves show that treatment caused them. Safety counts should be interpreted with the trial’s clinical context and full safety reporting, which is not completely available in the registry record.

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

The posted primary results show more negative mean changes in daily bowel movements for both telotristat etiprate groups than for placebo over the 12-week double-blind period. The sponsor’s reported comparisons are statistically separated from zero, with p < 0.001 for each active-treatment group versus placebo and 95% confidence intervals below zero. These statistics describe group-level evidence for a difference in average change under the reported analyses.

They do not mean that every participant had a reduction, that the same change occurred for each participant, or that the observed average difference is clinically important. The registry does not report a threshold for an important change in bowel movements. Statistical evidence and clinical importance are related but distinct questions. The record also does not provide individual outcome distributions that would show the range of responses or how many participants experienced particular changes.

The comparisons address each dose against placebo. They do not establish a difference between the two doses, and no direct dose comparison is reported. The secondary outcomes offer additional measures but do not all show the same degree of separation in the unadjusted results. Their interpretation is limited by the absence of sponsor-reported analyses and a reported multiplicity strategy.

These results are specific to the enrolled population, treatment period, endpoint definition, and analysis information in the registry. They do not by themselves establish what would happen in a different population, with a different treatment duration, or under different care conditions. Safety counts also require separate interpretation and do not establish causation. The registry record supports a careful description of the posted estimates and uncertainty, not a treatment recommendation or a claim about an individual participant’s outcome.

18. Why This Trial Matters Statistically

TELESTAR illustrates how a clinical trial can express a symptom outcome as a repeated daily measure and summarize change over a defined treatment period. The daily diary outcome is directly connected to the study objective, while the placebo group provides a concurrent comparator for interpreting the observed change. Randomization and masking are design features intended to reduce bias, although implementation details are not reported in the registry record.

The primary results also show why estimates and uncertainty should be read together. The mean differences give the direction and scale of the group contrasts, while confidence intervals show the range of uncertainty around those estimates. The sponsor’s reported rank-sum analyses and the simple recalculations from summary statistics are related but not identical methods; keeping them distinct helps prevent a supplementary calculation from being mistaken for the trial’s original analysis.

The secondary outcomes demonstrate another statistical lesson: evidence can vary across endpoints, and examining multiple outcomes without a reported adjustment makes isolated findings harder to interpret. Safety counts likewise require attention to group context, especially when an open-label extension is reported alongside randomized treatment groups. Finally, planning illustrations based on observed effects can clarify how smaller assumed effects require more participants, but they cannot stand in for the original design rationale.

Taken together, the record offers a useful example of interpreting a primary endpoint, group contrast, confidence interval, secondary analyses, and safety counts without treating any single statistic as a complete account of a trial.

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 provides summary results rather than participant-level data. This prevents independent reproduction of the sponsor’s Wilcoxon rank sum analyses and limits assessment of distributions, outliers, diary completion, and the relation between repeated observations. The record does not report how missing primary or secondary outcome data were handled, or whether sensitivity analyses assessed the effect of missingness.

The method description for the primary outcome identifies a rank-sum test and reports a mean difference, but does not provide full detail on the calculation of the estimate and confidence interval. The record also does not report a complete statistical analysis plan, multiplicity procedure, interim analyses, or the original sample-size assumptions. Those aspects cannot be reconstructed from the posted results.

The secondary outcomes have varying numbers of participants with available values, and the reasons for that variation are not reported in the registry record. Sponsor-reported inferential analyses are not posted for those endpoints. Their unadjusted re-calculations are therefore less conclusive, especially in the absence of a reported testing hierarchy or multiplicity strategy.

The record describes an open-label extension, but the safety counts do not provide full detail on event timing, duration of observation, attribution, or overlap among categories. Extension participants are not directly comparable with the randomized double-blind groups. The registry also does not report a clinical-importance threshold for the primary endpoint, limiting interpretation of the practical meaning of the estimated differences. These limitations constrain independent evaluation without invalidating the reported descriptive results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: TELESTAR (Telotristat Etiprate for Somatostatin Analogue Not Adequately Controlled Carcinoid Syndrome) — NCT01677910.
• Registry record last updated 2018-02-27; status last verified 2018-01.
• Results first posted 2017-09-18.
• 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 identifies TELESTAR (NCT01677910) as a completed Phase 3, randomized, placebo-controlled, parallel-group, multicenter, double-blind study sponsored by Lexicon Pharmaceuticals. Enrollment was 135. The recorded start date was 2013-01-08 and primary completion date was 2016-03-21.

The primary outcome was change from baseline in daily bowel movements averaged over the 12-week double-blind period. The registry reports more negative group mean changes for both telotristat etiprate doses than for placebo, with sponsor-reported comparisons of each dose against placebo and p < 0.001 for both.

Three secondary outcomes and adverse-event counts are also posted. The registry does not report a multiplicity strategy, full missing-data methods, or the original trial sample-size assumptions. The secondary recalculations are unadjusted and should be read with those limitations in mind.