A Study of TAK-954 to Treat Gastrointestinal Dysfunction in Adults After Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of TAK-954 to Treat Gastrointestinal Dysfunction in Adults After Surgery (NCT03827655), a randomized phase 2 study. The primary outcome is Time From End of the Surgery to Resolution of Upper and Lower Gastrointestinal (GI) Function Postsurgery as Assessed by the Investigator.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase 2 dose-ranging study of intravenous TAK-954 for prophylaxis and treatment of postoperative gastrointestinal dysfunction. The official title describes it as double-blind and placebo-controlled; the registry’s masking classification is quadruple. The record does not explain how those masking descriptions relate to one another. Takeda is listed as the sponsor.

Enrollment was 209, and the study status is completed. The recorded start date is 2019-03-07 and the primary completion date is 2022-05-27. Participants undergoing large- or small-bowel resection were assigned to placebo or one of the TAK-954 regimens. The treatment descriptions specify a 60-minute intravenous infusion before surgery on Day 1, followed by daily postsurgery treatment until return of upper and lower gastrointestinal function or for up to 10 days. For the combination regimens, TAK-954 was given presurgery and placebo infusions were given postsurgery.

The primary efficacy analysis used the FAS: randomized participants who received at least 1 dose of study drug and had at least 1 valid postbaseline on-treatment primary efficacy evaluation, defined as bowel movement or tolerance of solid food. The primary outcome was time from the end of surgery to resolution of both upper and lower gastrointestinal function, assessed by the investigator. Kaplan-Meier survival analysis was used. The record lists 10 outcome measures and 18 analyses. Details of the original sample-size justification, intended interim analyses, and full statistical analysis plan 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: Participants with a diagnosis of postoperative gastrointestinal dysfunction were enrolled in a 1:1:1:1:1 ratio into one of the five treatment groups to receive TAK-954 and/or placebo before and after surgery.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all participants who were randomized, received at least 1 dose of study drug, and had at least 1 valid postbaseline on-treatment primary efficacy evaluation (bowel movement or tolerating solid food).

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: Randomized Set included all participants who were randomized in the study.

6. Primary Endpoint

The registry lists the primary outcome as Time From End of the Surgery to Resolution of Upper and Lower Gastrointestinal (GI) Function Postsurgery as Assessed by the Investigator, measured over Day 1 (surgery) up to Day 10 postsurgery.

The primary endpoint measures the elapsed time from the end of surgery until both components of gastrointestinal recovery have occurred. The upper gastrointestinal component was tolerance of solid food without first occurrence of vomiting or clinically significant nausea for 1 calendar day after a solid meal. The lower gastrointestinal component was the first spontaneous bowel movement. The resolution time was defined by whichever of those two events occurred later, with observation extending from Day 1 (surgery) up to Day 10 postsurgery.

A time-to-event endpoint is useful when the timing of recovery matters and participants may reach the event at different times. It preserves information about when the event occurs rather than reducing recovery to a simple yes-or-no status at a single assessment point. Kaplan-Meier analysis was used for this endpoint. In general, this method estimates the event-time pattern while allowing for participants whose event time is not observed through the end of follow-up; the registry record does not report the details of censoring or missing-time handling in this analysis.

The arm results are reported as medians with full ranges. A median describes the midpoint of the observed or estimated event-time distribution, while the full range conveys the lowest and highest reported values. Neither the median nor the range alone describes the precision of a treatment comparison. The sponsor’s reported hazard ratios and their confidence intervals address comparative time-to-event evidence separately. The endpoint is investigator-assessed, and the record does not report further information on adjudication or assessment procedures.

7. Results Posted in the Registry

• Placebo vs TAK-954 0.5 mg/100 mL: hazard ratio 0.92 (95% CI 0.63–1.33), reported p = =0.649 (as reported in the registry).
• Placebo vs TAK-954 0.5 mg/100 mL + Placebo: hazard ratio 1.00 (95% CI 0.69–1.43), reported p = =0.505 (as reported in the registry).

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.

Time From the End of the Surgery (Time the Incision is Closed) Until Ready for Discharge as Assessed by the Investigator

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Wald chi-square test); it was not recalculated.
• Result:
  • Placebo vs TAK-954 0.5 mg/100 mL: hazard ratio 1.03 (95% CI 0.71–1.49), reported p = =0.449 (as reported in the registry).
  • Placebo vs TAK-954 0.5 mg/100 mL + Placebo: hazard ratio 1.00 (95% CI 0.69–1.44), reported p = =0.507 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL + Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Time From the End of Surgery Until the Discharge Order is Written

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Wald chi-square test); it was not recalculated.
• Result:
  • Placebo vs TAK-954 0.5 mg/100 mL: hazard ratio 1.05 (95% CI 0.73–1.52), reported p = =0.406 (as reported in the registry).
  • Placebo vs TAK-954 0.5 mg/100 mL + Placebo: hazard ratio 0.77 (95% CI 0.54–1.11), reported p = =0.880 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL + Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Time From the End of Surgery to Discharge From Hospital

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Wald chi-square test); it was not recalculated.
• Result:
  • Placebo vs TAK-954 0.5 mg/100 mL: hazard ratio 1.03 (95% CI 0.72–1.48), reported p = =0.446 (as reported in the registry).
  • Placebo vs TAK-954 0.5 mg/100 mL + Placebo: hazard ratio 0.76 (95% CI 0.53–1.09), reported p = =0.892 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo vs TAK-954 0.5 mg/100 mL + Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of recovery, including discharge readiness and timing, return of bowel function, solid-food tolerance, prolonged postoperative gastrointestinal dysfunction, nasogastric-tube use, and first flatus. They extend the primary endpoint by separating its components and adding milestones relevant to recovery and hospital discharge. The reported secondary time summaries do not form a single uniform pattern across every measure and treatment regimen; each outcome captures a distinct event with its own assessment and follow-up period.

These measures relate to the primary result because they help describe whether the pattern for combined resolution is reflected in other recovery milestones. They cannot be treated as interchangeable: discharge readiness, actual discharge, tolerance of solid food, and bowel movement are different events. A difference in one outcome would not, on its own, establish a difference in the combined primary endpoint, and the absence of a clear primary separation does not determine every secondary result.

The registry lists 9 posted secondary outcomes. The available secondary analyses include sponsor-reported hazard ratios for certain comparisons, while other listed results are presented as arm-level summaries. Each secondary finding should be viewed in its own context, including its population, endpoint definition, and uncertainty. The registry record does not report a multiplicity adjustment or a testing hierarchy covering these outcomes.

When many outcomes and comparisons are examined, some may appear noteworthy by chance. Unadjusted secondary results therefore carry less weight than a prespecified primary analysis, particularly when the analysis plan and multiplicity strategy are not reported. These results can describe the range of recovery measures assessed and may inform further research, but they should not be read as independent confirmation of the primary result or as definitive evidence from a family of tests.

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

• Time From the End of the Surgery (Time the Incision is Closed) Until Ready for Discharge as Assessed by the Investigator
• Time From the End of Surgery Until the Discharge Order is Written
• Time From the End of Surgery to Discharge From Hospital
• Time From End of Surgery to Tolerance of Solid Food as Assessed by the Investigator
• Time From End of Surgery to First Spontaneous Bowel Movement as Assessed by the Investigator
• Percentage of Participants With Postoperative Gastrointestinal Dysfunction (POGD) >= 5 Days as Assessed by the Investigator
• Percentage of Participants Requiring Insertion of Nasogastric (NG) Tube Postsurgery
• Time From End of Surgery to First Flatus

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. Each participant’s event is resolution of both upper and lower gastrointestinal function, with the later of the two defined events determining the endpoint time. Kaplan-Meier survival analysis was used. In general, Kaplan-Meier methods estimate the probability that the event has not yet occurred over time, using the observed event times and accounting for censoring. Censoring means that an event time is not fully observed during the available follow-up. The registry record does not report the operational rules for censoring, the number censored, or how missing assessments were handled.

The arm summaries are medians with full ranges. The median is a central summary of event time and is less affected by very long values than an arithmetic mean. The full range records the minimum and maximum values, but does not show the distribution of observations between those extremes. A range is not a confidence interval. The registry record does not provide confidence intervals for the arm medians in the posted primary outcome results.

The sponsor’s comparative analyses are reported as hazard ratios, using Wald chi-square tests. In general, a hazard ratio compares event rates over follow-up between groups under the model used for the analysis. A ratio of 1 corresponds to equal estimated hazards under that comparison; values on either side indicate a relative difference, but interpretation requires knowing the comparison order and event coding. The reported confidence intervals express uncertainty around the estimated ratio. The registry record does not give further details of the hazard model, such as covariate adjustment or assumptions about proportional hazards, so those features should not be inferred.

The primary comparisons use placebo against TAK-954 0.5 mg/100 mL and against TAK-954 0.5 mg/100 mL + Placebo. Both are identified as superiority analyses, and both use the Wald chi-square test. The p-values and confidence intervals describe evidence for those specified comparisons; they do not automatically address every dose or every possible contrast among the five listed arms. The record does not report the full analysis plan or whether other comparisons were prespecified.

The primary efficacy population was the FAS, defined as randomized participants who received at least 1 dose of study drug and had at least 1 valid postbaseline on-treatment primary efficacy evaluation, based on bowel movement or solid-food tolerance. This definition is narrower than simply all participants enrolled or randomized. The reported primary endpoint group sizes were 45 for placebo, 23 for TAK-954 0.1 mg/100 mL, 42 for TAK-954 0.5 mg/100 mL, 21 for TAK-954 0.1 mg/100 mL + Placebo, and 44 for TAK-954 0.5 mg/100 mL + Placebo. Reasons that participants might not meet the FAS definition, and the numbers excluded for each reason, are not reported in the registry record.

General interpretation of confidence intervals is important for both the hazard ratios and the medians. A confidence interval represents uncertainty about an estimate under the analysis method and assumptions; it is not a range containing a fixed proportion of individual participant outcomes. A wide interval indicates less precision, while an interval that includes the no-difference value does not provide a clear distinction from that value at the corresponding confidence level. The reported hazard-ratio intervals are 90% confidence intervals. The registry record does not report whether those intervals were adjusted for multiple comparisons.

The secondary outcomes include time to investigator-assessed readiness for discharge, time to a written discharge order, time to hospital discharge, time to solid-food tolerance, time to first spontaneous bowel movement, postoperative gastrointestinal dysfunction lasting at least 5 days, postsurgery nasogastric-tube insertion, and time to first flatus. Several secondary time outcomes are also reported as medians with full ranges and have sponsor-reported hazard-ratio comparisons. These outcomes address related but distinct aspects of postoperative recovery.

Multiplicity arises when many outcomes or comparisons are tested. In general, the more statistical tests considered together, the greater the chance of at least one apparently notable result arising by chance if no adjustment or hierarchy is used. The registry record lists 10 outcome measures and 18 analyses, but does not report a multiplicity adjustment strategy or a confirmatory testing hierarchy. Therefore, secondary comparisons should be treated as exploratory unless a more complete analysis plan establishes otherwise. The original sample-size justification and interim-analysis procedures are also not reported in the registry record.

11. Confidence Intervals and Precision

The primary sponsor-reported hazard-ratio estimates are accompanied by 90% confidence intervals. For Placebo vs TAK-954 0.5 mg/100 mL, the estimate is 0.92 and the interval is 0.63 to 1.33. For Placebo vs TAK-954 0.5 mg/100 mL + Placebo, the estimate is 1.00 and the interval is 0.69 to 1.43. Each interval includes 1, the no-relative-difference value for a hazard ratio. The estimates therefore do not sharply distinguish either comparison from that value, but the intervals also span values on both sides of it.

Precision concerns how narrowly an estimate is determined by the data and analysis. A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it show the distribution of individual recovery times. It describes uncertainty in the estimated group contrast under the method used. The primary intervals permit more than one interpretation of the relative event rate; they do not establish equality between groups. No equivalence margin is reported in the registry record.

The group medians also need to be read with their full ranges. The ranges vary across arms and overlap, but ranges are descriptive summaries rather than formal measures of uncertainty. The registry record does not report confidence intervals for the medians. The primary efficacy group sizes differ across arms, and the group estimates are based on the participants included in that analysis population.

Overall, the reported comparisons are not precise enough to support a narrow conclusion about the size of any difference. The interval estimates should be considered with the endpoint definition, analysis population, and phase 2 design. Additional details on the hazard model, censoring, missing data, and multiplicity would help a reader assess the estimates’ assumptions and interpretation; those details are not reported in the registry record.

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 use the observed effect as a starting point and show alternative targets at 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For time-to-event outcomes, the displayed requirements are total numbers of events, not participants per arm. The primary endpoint’s planning figures are 4,516 total events for 80% power and 6,046 total events for 90% power at 100% of the observed effect; planning for 75% of the observed effect gives 8,028 and 10,748 total events, and planning for 50% gives 18,063 and 24,182 total events.

The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The time-to-event calculations use the Schoenfeld method. The effect to detect is the stated fraction of the observed effect. These are planning calculations based on the observed effect, not the trial’s original design assumptions; the original sample-size justification is not reported in the registry record.

In plain terms, the 80% power column represents the planned event count under which the calculation has an 80% chance of detecting the specified effect at the stated significance level, assuming the planning model applies. The 90% column applies the same idea at a higher target probability. A smaller effect is harder to distinguish from random variation, so detecting a smaller effect generally requires more events and, in a time-to-event study, may require a larger study population or longer observation. The required numbers are not the observed power of this completed trial.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.920, so ln(HR) = -0.0834.
2. d = 4 × (1.96 + 0.842)² / [ln(0.920)]² = 4,515.7, rounded up to 4,516 events in total 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
hr <- 0.92                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(3827655)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 4,516 (80% power), 6,046 (90% power)
 75% of observed effect: events = 8,028 (80% power), 10,748 (90% power)
 50% of observed effect: events = 18,063 (80% power), 24,182 (90% power)
Simulated power with 4,516 events: 0.800 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 6,123 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 209 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 0.0621369863013699          # control-arm median, months (converted from the posted unit)
hr          <- 0.92          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
     Analysis               Value Efficacy
    IA 1: 33%                   Z   3.7103
      N: 2066         p (1-sided)   0.0001
 Events: 2039        ~HR at bound   0.8485
     Month: 8    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.92   0.0338
    IA 2: 67%                   Z   2.5114
      N: 4106         p (1-sided)   0.0060
 Events: 4078        ~HR at bound   0.9244
    Month: 16    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.92   0.5603
        Final                   Z   1.9930
      N: 6124         p (1-sided)   0.0231
 Events: 6117        ~HR at bound   0.9503
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.92   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor’s own primary comparisons are the hazard ratios from the Wald chi-square analyses, with 90% confidence intervals and reported p-values. For placebo compared with TAK-954 0.5 mg/100 mL, the sponsor reports a hazard ratio of 0.92, a confidence interval of 0.63 to 1.33, and p =0.649. For placebo compared with TAK-954 0.5 mg/100 mL + Placebo, the sponsor reports a hazard ratio of 1.00, a confidence interval of 0.69 to 1.43, and p =0.505.

The comparisons presented in the posted results match the sponsor-reported analyses; no discrepancy is flagged. These sponsor estimates take precedence over any simple recalculation from summary statistics, because the sponsor’s time-to-event analysis uses participant-level information that cannot be reconstructed from the arm medians and ranges alone. No recalculated primary hazard ratio is needed to interpret the posted results.

For readers, the important distinction is that the arm medians describe typical times, while the hazard ratios compare event patterns over follow-up under the sponsor’s analysis. The record identifies the test and reported estimates but does not provide all model details. The hazard-ratio results should therefore be interpreted as reported, without attempting to infer unreported adjustments or analysis assumptions.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and several secondary outcomes, with 10 outcome measures and 18 analyses listed. It does not report how the study controlled the overall risk of false-positive findings across those outcomes, dose groups, and comparisons. No multiplicity adjustment method or ordered testing hierarchy is reported. Without that information, a nominal p-value from an individual secondary analysis should not be interpreted as if it were the only test undertaken.

The primary efficacy population is defined as randomized participants who received at least 1 dose and had at least 1 valid postbaseline on-treatment primary efficacy evaluation. This provides an explicit inclusion rule, but the record does not state the number excluded from the primary analysis or give reasons for exclusion. It also does not report detailed missing-data handling, imputation procedures, sensitivity analyses, or the censoring rules used for the time-to-event analyses.

Randomization and masking are listed, but details of sequence generation, allocation concealment, and implementation are not reported in the registry record. The official title calls the study double-blind, while the registry classification lists quadruple masking; the record does not explain that terminology. The study is described as randomized and parallel-group, but those labels alone do not resolve questions about analysis assumptions or missing observations.

The original sample-size rationale, any planned interim analyses, and the complete statistical analysis plan are not reported in the registry record. As a result, readers cannot verify from the record alone whether all listed analyses were planned before outcome data were examined, how subgroup or dose comparisons were prioritized, or what rules governed stopping or adjustment. These omissions limit assessment of the full inferential framework, especially for secondary results, while leaving the stated primary endpoint definition and sponsor-reported comparisons available for interpretation.

17. 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: postoperative ileus (10.0%), anastomotic leak (4.1%), acute kidney injury (4.0%), hip fracture (4.0%), acute respiratory failure (3.8%).

Safety counts are reported separately from the primary efficacy analysis population. Across the five safety groups, the numbers at risk for serious adverse events were 49, 26, 48, 25, and 50, respectively. The corresponding numbers affected were 8, 9, 8, 2, and 11. Deaths reported were 0 in placebo, 0 with TAK-954 0.1 mg/100 mL, 0 with TAK-954 0.5 mg/100 mL, 0 with TAK-954 0.1 mg/100 mL + Placebo, and 1 with TAK-954 0.5 mg/100 mL + Placebo.

The registry also lists serious adverse-event terms, including postoperative ileus at 10.0%, anastomotic leak at 4.1%, acute kidney injury at 4.0%, hip fracture at 4.0%, acute respiratory failure at 3.8%, and drug reaction with eosinophilia and systemic symptoms at 3.8%. These terms and percentages are reported in the record; they do not establish that an event was caused by study treatment. The record does not provide context for each event’s timing, severity, outcome, or treatment attribution in the listed summary.

Counts should be read with their group-specific numbers at risk and the study’s phase 2 context. They are descriptive safety data, not a formal demonstration that groups have equal or different risk. Interpretation also depends on event definitions and follow-up, details that are not reported in the registry record.

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

The posted results describe a randomized phase 2 comparison of placebo and several intravenous TAK-954 regimens in adults undergoing small- or large-bowel resection. The primary endpoint focuses on the time until both upper and lower gastrointestinal function have returned, using a combined event definition and investigator assessment. The reported arm medians and sponsor hazard ratios provide a view of recovery timing and comparative uncertainty for the specified groups.

The sponsor’s two primary comparisons have 90% confidence intervals that include 1, and their reported p-values are =0.649 and =0.505. Those results do not give a clear statistical separation in the specified comparisons. They also do not demonstrate that the groups are equivalent, exclude all potentially meaningful effects, or establish that every dose regimen has the same effect. The registry record does not identify an equivalence or noninferiority framework.

The evidence is bounded by the endpoint’s definition, the FAS eligibility criteria, the reported group sizes, and the available analysis details. The primary measure combines two recovery milestones, so it does not answer every question about eating, bowel movement, or discharge separately. Secondary outcomes add context but involve multiple measures, and the record does not report a strategy for adjustment across those analyses.

Safety counts and serious adverse-event terms are descriptive. They should be considered as reported, without inferring causation or drawing a definitive comparative safety conclusion from counts alone. More broadly, a completed phase 2 study with imprecise comparative estimates can inform understanding of the evidence and the uncertainties that remain. It does not, by itself, settle the effect of TAK-954 in other settings or populations. No medical recommendation follows from these registry results.

19. Why This Trial Matters Statistically

This study illustrates the statistical challenge of comparing time to recovery after surgery. The outcome is not simply whether gastrointestinal function returns; it is when both upper and lower function meet specified criteria. Choosing the later event makes the endpoint clinically distinct from either component alone and changes what the estimate represents. A reader therefore needs the event definition before interpreting the median or hazard ratio.

It also shows why arm summaries and comparative analyses answer different questions. Medians and full ranges describe the observed or estimated time distribution within groups, while a hazard ratio summarizes a comparison over time under a statistical model. Their interpretation depends on follow-up, event definition, and model assumptions. The posted primary comparisons include confidence intervals, allowing the uncertainty around those ratios to be considered rather than relying only on point estimates or p-values.

The study includes several active regimens, two forms of presurgery/post-surgery treatment sequencing, and multiple secondary recovery milestones. That breadth is useful for characterizing the clinical questions addressed, but it also makes prespecification and multiplicity important. The registry record does not report the full analysis plan or the approach to multiplicity, so secondary signals require particular caution.

Finally, the record distinguishes enrollment from the primary efficacy population and gives a specific FAS definition. This reinforces the importance of understanding who contributes to an endpoint analysis. Transparent reporting of exclusions, missing data, censoring, and model assumptions would make the estimates easier to appraise. The posted information supports a careful reading of the primary comparisons while leaving important design and analysis details unresolved.

20. 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.

Several limitations specific to this study affect interpretation. The primary endpoint combines tolerance of solid food and first spontaneous bowel movement, using the later event as the time to resolution. This construction is relevant to combined recovery but does not identify which component drives a group-level pattern. The endpoint is assessed by the investigator, and assessment or adjudication details are not reported in the registry record.

The primary efficacy population excludes participants who did not meet the stated FAS criteria, but the record does not report the number or reasons for any exclusions. Detailed missing-data and censoring procedures are also not reported. Those details matter for time-to-event estimates because incomplete follow-up and absent assessments can affect which event times contribute to the analysis.

The sponsor reports hazard ratios and 90% confidence intervals, but the record does not describe the hazard model’s covariates, assumptions, or diagnostics. The interval estimates include 1, and the group sizes in the primary analysis vary. The record also does not report the original sample-size rationale, interim analyses, or the complete statistical analysis plan. The planning illustrations based on observed effects cannot substitute for the study’s original design justification.

Multiple outcomes and analyses are listed, but multiplicity control is not reported. Consequently, secondary results are harder to interpret as confirmatory findings. The masking classification and the official title’s double-blind wording are not reconciled in the record. Safety data are reported as counts and event terms without full contextual details or attribution in the summary. These limitations do not erase the posted results, but they constrain how specifically those results can be interpreted.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of TAK-954 to Treat Gastrointestinal Dysfunction in Adults After Surgery — NCT03827655.
• Registry record last updated 2023-06-23; status last verified 2023-05.
• Results first posted 2023-06-23.
• 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.

24. Record Summary

NCT03827655 is a completed randomized, parallel-group phase 2 study sponsored by Takeda. It enrolled 209 participants undergoing large- or small-bowel resection and evaluated intravenous TAK-954 regimens against placebo. The official title describes a double-blind study, while the registry masking classification is quadruple.

The primary endpoint was time from the end of surgery to resolution of upper and lower gastrointestinal function, assessed by the investigator and analyzed using Kaplan-Meier survival analysis. The sponsor reported two primary hazard-ratio comparisons, both with 90% confidence intervals that include 1. The registry also lists secondary recovery outcomes and descriptive safety counts.

Important details—including the original sample-size justification, interim-analysis procedures, multiplicity strategy, and several aspects of missing-data and model handling—are not reported in the registry record. The posted estimates therefore support a cautious interpretation centered on the stated endpoint and reported comparisons.