Tranexamic Acid for The Treatment of Gastrointestinal Bleeding: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tranexamic Acid for The Treatment of Gastrointestinal Bleeding (NCT03540368), a randomized na study. The primary outcome is Re-bleeding.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial comparing tranexamic acid injection with placebo for gastrointestinal bleeding. The registry record reports enrollment of 48, a start date of 2018-07-01, primary completion on 2019-03-01, and a completed status. The recorded phase is NA, and Universitas Indonesia is listed as the sponsor.

The registry title describes the study as randomized, double-blind, and controlled, while the masking field records single masking. These descriptions do not fully align; further detail about who was masked and how masking was implemented is not reported in the registry record. Allocation is recorded as randomized, and the model as parallel. The record does not report the randomisation method, allocation concealment procedures, or whether the groups were balanced on baseline characteristics.

The posted outcome results give the tranexamic-acid arm as 19.0 participants and the placebo arm as 23.0 participants. These arm-level denominators are the ones attached to the outcomes; the registry record does not explain the difference between the enrollment figure and the denominators in the posted results. It also does not report the original design assumptions, a sample-size justification, or details of the protocol beyond the information recorded for the trial.

The primary outcome was re-bleeding, measured as the number of participants experiencing the event within 28 days after randomisation. All-cause mortality within 30 days after randomisation was the posted secondary outcome. These distinct observation periods matter when interpreting the outcomes: the reported re-bleeding result concerns a specified 28-day window, while the mortality result concerns a 30-day window.

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: Excluded because clinically had CKD

Overall Study

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 Re-bleeding, measured over 28 days after randomisation.

The primary endpoint counts participants who experienced re-bleeding within 28 days after randomisation. It is a binary outcome at the participant level: each participant is classified according to whether the event occurred during that follow-up period. The registry record describes the measure as the number of participants experiencing re-bleeding in each arm.

Re-bleeding is used to represent recurrence of bleeding after randomisation, making it a direct clinical event relevant to the trial's stated question about treatment for gastrointestinal bleeding. A participant count is relatively straightforward to interpret, but it does not describe when within the follow-up period re-bleeding occurred, how severe it was, or how many recurrent episodes any participant experienced. Those details are not reported in the registry record.

For this endpoint, 6.0 participants in the tranexamic-acid arm and 7.0 in the placebo arm were recorded as experiencing re-bleeding. The posted comparison expresses the difference between the arm-level risks as a risk difference, with the tranexamic-acid arm as the comparison arm. The event counts and estimated contrast should be read together: the counts show what was observed, while the estimate and its confidence interval describe the uncertainty around the between-arm comparison. The endpoint alone does not establish that any observed difference is caused by treatment.

7. Results Posted in the Registry

• Tranexamix Acid Group: 31.6% (6/19) versus 30.4% (7/23) on control; risk difference 1.1 percentage points (95% CI -27.0 to 29.3), risk ratio 1.04 (0.42–2.57); unadjusted two-proportion z-test p = 0.936.

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.

All Cause Mortality

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tranexamix Acid Group: 21.1% (4/19) versus 21.7% (5/23) on control; risk difference -0.7 percentage points (95% CI -25.6 to 24.2), risk ratio 0.97 (0.30–3.11); unadjusted two-proportion z-test p = 0.957.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tranexamix Acid Group and the control. The interval gives the range of effects that remain compatible with the data.

The only posted secondary endpoint is all-cause mortality within 30 days after randomisation. Its overall pattern is similar to the primary result in the key statistical sense: the estimate is imprecise, and the confidence interval includes the null value. The mortality comparison therefore does not provide a precise, independent resolution of the uncertainty around the re-bleeding result.

Secondary outcomes can add context because they assess a different event and follow-up period. They should not be treated as interchangeable with the primary outcome: re-bleeding is measured within 28 days after randomisation, while mortality is measured within 30 days. A result for one does not establish the result for the other, and the registry record does not report a combined endpoint that would merge them.

Unadjusted secondary results generally carry less confirmatory weight when multiple outcomes or analyses may be considered. In general, examining more comparisons increases the chance that an apparently notable result could arise by chance. The registry record lists one secondary outcome, but it does not report a multiplicity strategy, a hierarchy among outcomes, or whether additional outcomes were analyzed but not posted. No adjusted secondary analyses are reported.

The secondary outcome is therefore best read as supporting descriptive context rather than as decisive evidence for or against the primary comparison. Its interpretation should account for its uncertainty and its status as a secondary outcome. The registry record does not report the analysis population or missing-data handling for this endpoint, so those details cannot be used to refine the interpretation.

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

• All Cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either experienced re-bleeding within the specified follow-up period or did not. The posted results give event counts and arm denominators, then express the comparison using a risk difference, a risk ratio, and an odds ratio. These measures describe the same underlying outcome from different perspectives; they are not independent pieces of evidence.

What does a risk difference describe?

A risk difference subtracts the event risk in one arm from the event risk in the other. It is an absolute contrast, so zero represents no difference between arms. The posted primary risk difference is 0.011. Its confidence interval runs from -0.270 to 0.293, so it includes zero and values on either side. The interval is a range of estimates compatible with the data under the method's assumptions; it is not a range in which the true value is guaranteed to lie.

How do relative measures differ?

A risk ratio compares the event risks by division, while an odds ratio compares the odds of the event. For each measure, one is the null value indicating no relative difference. The primary risk ratio is 1.038, with a confidence interval from 0.420 to 2.566; the primary odds ratio is 1.055, with a confidence interval from 0.284 to 3.923. Both intervals include one. Relative measures can be useful for comparing proportional contrasts, while a risk difference expresses an absolute contrast. The choice of measure affects how an estimate is communicated, not the observed event counts.

What does a confidence interval add?

A confidence interval communicates uncertainty around an estimate. In general, it reflects both the observed data and the statistical procedure used to construct it. A narrower interval indicates greater precision than a wider interval, while the interval's position indicates which contrasts are compatible with the data under the method. The registry record does not report the interval-construction method, so that detail should not be inferred.

What does the p-value say?

The primary comparison has an unadjusted p-value of 0.936. In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of a statistical test. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or importance of an effect. The posted value is explicitly unadjusted; the registry record does not report whether any multiplicity adjustment was used in analyses outside the posted results.

Why do counts and model-based contrasts both matter?

Counts make the observed events concrete, and the denominators show the group sizes used for the outcome. A contrast and its interval then provide a comparative estimate with uncertainty. Neither the estimate nor its p-value replaces the underlying event counts. Because the outcome is binary, methods for continuous measurements such as comparing means are not the relevant description of the posted result. The registry record does not report the named test or model used for the comparisons, any covariate adjustment, or analysis-population definitions.

The posted mortality comparison uses the same types of binary-outcome measures. Its risk difference is -0.007, with a confidence interval from -0.256 to 0.242; the risk ratio is 0.968, with a confidence interval from 0.302 to 3.108; and the odds ratio is 0.96, with a confidence interval from 0.218 to 4.228. These measures all have intervals that include their respective null values. The posted figures are unadjusted, and the record lists no reported analyses. It is therefore not possible to determine from the registry record whether these calculations match a prespecified analysis plan or whether other analyses were undertaken.

In general, statistical significance is not the same as clinical importance, and failure to meet a conventional significance threshold does not establish that groups are alike. Interpretation needs to consider the estimate, the interval, the event counts, the endpoint definition, and the analysis context. For this trial, the broad intervals are especially important because they leave substantial uncertainty about the possible size and direction of the differences.

11. Confidence Intervals and Precision

The confidence intervals for both posted outcomes are broad and include the null value. For re-bleeding, the risk difference is 0.011, with a confidence interval from -0.270 to 0.293. For all-cause mortality, the risk difference is -0.007, with a confidence interval from -0.256 to 0.242. In each case, the observed estimate is only one point within a range that spans contrasts in both directions.

Precision describes how narrowly the data locate an effect estimate. A wide interval indicates that the estimate remains uncertain; it does not mean that every value inside the interval is equally plausible, and it does not guarantee that the true effect lies within the interval. These intervals do not support a precise claim of no difference. They also do not isolate a single direction of effect.

The relative estimates reinforce this caution. For primary re-bleeding, the risk-ratio interval is 0.420 to 2.566 and the odds-ratio interval is 0.284 to 3.923. For mortality, the risk-ratio interval is 0.302 to 3.108 and the odds-ratio interval is 0.218 to 4.228. Each interval includes one, the null value for a ratio measure, and spans a wide range.

The registry record does not report the confidence-interval construction method. The intervals should therefore be interpreted as posted, without assuming a particular calculation procedure. In practical terms, the estimates are not precise enough to distinguish small contrasts from larger ones with confidence.

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 display gives illustrative participants per arm, not a target total across both arms. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a planning reference and considers detecting the stated fraction of that effect. The original trial's own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true effect and the assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not guarantees about what a future trial will find. The figures are not observed power.

Rows describe planning for 100%, 75%, or 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning illustration requires more participants per arm as the effect fraction gets smaller. This relationship is a general feature of statistical planning, not evidence that any particular effect size is correct.

The sample-size calculations are illustrations based on the observed result, not a reconstruction of the study's original design. Estimates derived from a small trial can be uncertain, so planning directly from an observed effect should be treated cautiously. The registry record does not state that these illustrative figures were used to plan the 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

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 = 0.304; treatment proportion p₁ = 0.316; average p̄ = 0.310.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6541 = 1.2820.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6541 = 0.5505.
4. n = (1.2820 + 0.5505)² / (0.0114)² = 25,651.0, rounded up to 25,652 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 <- 0.304347826086957                          # control proportion
p1 <- 0.315789473684211                          # 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(3540368)
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 = 25,652 (80% power), 34,339 (90% power)
 75% of observed effect: n per arm = 45,487 (80% power), 60,893 (90% power)
 50% of observed effect: n per arm = 102,083 (80% power), 136,659 (90% power)
power.prop.test: 25651 
Simulated power at n = 25,652 per arm: 0.796 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses multiple outcomes, time points, treatment contrasts, or analytic approaches. In general, the more statistical tests considered, the greater the chance of at least one apparently unusual result arising by chance. A prespecified outcome hierarchy or adjustment method can help define how such results should be interpreted. The registry record does not report a multiplicity strategy, an adjustment method, or a hierarchy for interpreting the primary and secondary outcomes.

The registry record lists re-bleeding as the primary endpoint and all-cause mortality as a secondary endpoint. It reports no analyses in the analysis listing. This absence means the registry record does not describe a full analysis plan, nor does it establish that no analyses were conducted. Details about the statistical test, covariate adjustment, interim analyses, subgroup analyses, and any prespecified handling of multiple comparisons are not reported in the registry record.

Missing-data handling is also not reported. The posted denominators are 19.0 participants in the tranexamic-acid arm and 23.0 participants in the placebo arm for the reported outcomes, but the record does not explain whether all enrolled participants contributed to each outcome, whether any outcome status was unknown, or how such cases were handled. Missing outcomes can affect both the event counts and the uncertainty of a comparison; without the relevant information, the direction or size of any effect cannot be assessed.

The analysis populations are not described. The record does not state whether results follow an intention-to-treat, per-protocol, or other population definition, or whether participants were analyzed according to their randomised arm. These details matter because exclusions after randomisation can affect the comparability created by random allocation. Interpretations should therefore be restricted to the posted counts and estimates, without assuming unreported procedures.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: thromboembolism (5.3%).

The registry record reports serious adverse events affecting 1 participant in the tranexamic-acid arm, with 19 at risk, and 1 participant in the placebo arm, with 23 at risk. Other adverse events are reported for 0 participants in each arm, with 19 and 23 at risk, respectively. These are event counts as recorded; they do not by themselves establish whether the groups differ in safety.

The record lists Thromboembolism as a top serious-event term at 5.3%. It does not provide enough detail in that entry to attribute the term to a particular arm or to describe its timing, severity, or relationship to treatment. The adverse-event summary should therefore be read as a limited registry report, not a complete assessment of all possible harms.

Deaths are recorded as 4 in the tranexamic-acid arm and 5 in the placebo arm. These figures also appear in the secondary all-cause mortality outcome, whose timeframe is 30 days after randomisation. The serious-event and mortality counts are distinct report types and should not be assumed to describe the same participants or events in the same way. The registry record does not report further safety-analysis methods or details about event ascertainment.

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

The posted results describe a randomized comparison of tranexamic acid injection and placebo for gastrointestinal bleeding. For the primary endpoint, the recorded re-bleeding counts are 6.0 and 7.0, respectively, within 28 days after randomisation. The estimated risk difference is 0.011, but its confidence interval extends from -0.270 to 0.293. This interval includes no difference and contrasts in either direction, so the result does not determine the direction or size of a treatment effect with precision.

The mortality outcome also remains uncertain. The posted risk difference is -0.007, with a confidence interval from -0.256 to 0.242. As with the primary result, the interval includes zero and covers possible differences in both directions. Neither outcome demonstrates equivalence, because the registry record does not report a margin defining how similar the arms would need to be to count as equivalent.

A large p-value does not prove that there is no effect. It means that the posted test did not identify strong evidence against its null comparison under the test's assumptions. The broad intervals show why that is not the same as a precise finding of no difference: the results remain compatible with a range of possible effects.

These findings should not be used to make a treatment recommendation. The registry record does not report important details such as eligibility criteria, baseline characteristics, the original analysis plan, missing-data procedures, or the full safety assessment. The conclusions that can be drawn are therefore limited to the posted event counts, estimates, and follow-up periods. The results describe uncertainty in this trial; they do not establish what would happen in other populations or settings.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a point estimate and a precise conclusion. The primary point estimate is close to zero, yet its confidence interval is broad and crosses zero. Looking only at the point estimate or the p-value would miss how much uncertainty remains about both the direction and magnitude of the between-arm contrast.

It also shows why event counts and denominators matter for interpreting binary outcomes. The counts identify the observed events, while the risk difference, risk ratio, and odds ratio express the comparison on different scales. None of these measures removes the uncertainty arising from limited information, and the measures should be read as alternative descriptions of the same outcome rather than as separate confirmations.

The planning illustrations emphasize another statistical distinction: a calculation based on an observed effect is not the same thing as the study's original sample-size plan. The registry record does not report the original planning rationale. The displayed planning figures can help explain how the assumed effect size relates to required participants per arm, but they cannot show that the trial was designed with those assumptions or that it had any particular observed power.

Finally, the record highlights the importance of reporting methods as well as results. Without details on analysis populations, missing outcomes, multiplicity, or the specific statistical procedures, readers cannot fully assess how the posted estimates were produced or how they relate to the original plan. Clear reporting of these elements is necessary for a complete appraisal of the strength and limits of clinical trial evidence.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific details needed to assess the results are not reported in the registry record. Eligibility criteria, participant characteristics, disease severity, and baseline comparability between arms are not described in the posted information. Without these details, the characteristics of the participants and the applicability of the results cannot be fully evaluated.

The record gives an enrollment figure of 48, while the outcome denominators are 19.0 and 23.0. It does not explain this relationship, report whether outcomes were missing, or state how participants with missing outcome information were handled. The analysis population is also not specified, so it is unclear whether the posted comparisons include all randomized participants or use another definition.

Important intervention and design details are absent. The dose, schedule, and duration for tranexamic acid injection are not reported. The record describes randomized allocation and a parallel model, but does not provide the randomisation procedure or allocation concealment details. Its title says double-blind, whereas the masking field records single masking; the record does not clarify this difference.

The statistical plan is not described in sufficient detail to determine the tests or models used, whether covariates were considered, how multiplicity was addressed, or whether interim analyses were planned or conducted. The original sample-size rationale is not reported. Safety reporting is also limited: details about event definitions, timing, severity, and attribution are not available. These gaps constrain interpretation and should not be filled by assumptions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Tranexamic Acid for The Treatment of Gastrointestinal Bleeding — NCT03540368.
• Registry record last updated 2026-03-27; status last verified 2026-03.
• Results first posted 2026-03-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed randomized, parallel-group trial of tranexamic acid injection versus placebo for gastrointestinal bleeding, sponsored by Universitas Indonesia. The record lists an enrollment of 48, a start date of 2018-07-01, and primary completion on 2019-03-01. Its title describes the trial as double-blind, while the masking field records single masking.

The primary endpoint was re-bleeding within 28 days after randomisation. The posted comparison is imprecise, with a risk-difference confidence interval that includes zero and extends in both directions. All-cause mortality within 30 days after randomisation was the posted secondary endpoint and is also uncertain.

The record does not report the original sample-size justification, analysis populations, missing-data handling, or a multiplicity strategy. The posted results therefore support a limited interpretation of the recorded outcomes, rather than a definitive conclusion about the size or direction of differences between the arms.