TRial to EvaluAte Tranexamic Acid Therapy in Thrombocytopenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TRial to EvaluAte Tranexamic Acid Therapy in Thrombocytopenia (NCT03136445), a randomized phase 3 study. The primary outcome is The Proportion of Patients Who Die or Have Bleeding of WHO Grade 2 or Above by WHO Criteria During the First 30 Days From the First Dose of Trial Treatment, or Planned First Dose for Those Participants Who do Not Receive Treatment..

2. Clinical Question

3. Trial Design

TRial to EvaluAte Tranexamic Acid Therapy in Thrombocytopenia (NCT03136445) is recorded as a phase 3, randomized, parallel-group trial comparing TXA with placebo. The registry record describes the study as double-blind in its official title and records masking as quadruple. It does not identify which specific groups or roles were covered by that masking designation.

The study enrolled 616 participants. The primary outcome results are reported for 298 participants in the intervention arm and 295 in the control arm. Safety results use different denominators: 300 in the intervention arm and 297 in the control arm for the listed adverse-event counts. These denominators reflect the populations reported for those results and should not be treated as interchangeable.

TXA was given by intravenous or oral administration, with the registry record describing different dose schedules by route. Placebo was saline for intravenous administration or an appearance-matched tablet for oral administration. The registry record lists NHS Blood and Transplant as sponsor and gives the study status as completed. The recorded study start is 2015-06, and primary completion is dated 2022-02-18.

The registry record does not report the original sample-size justification, the planned statistical analysis in full, or details of how participants were allocated to route of administration. Those aspects of the trial design cannot be inferred from the outcome results.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Participants with primary outcome data reported

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 The Proportion of Patients Who Die or Have Bleeding of WHO Grade 2 or Above by WHO Criteria During the First 30 Days From the First Dose of Trial Treatment, or Planned First Dose for Those Participants Who do Not Receive Treatment., measured over The first 30 days from first dose of trial treatment.

The primary endpoint combines two outcomes: death or bleeding of WHO Grade 2 or greater during the first 30 days from the first dose of trial treatment. For participants who did not receive treatment, the planned first dose defines the start of the timeframe. A participant meeting either part of the definition counts toward the composite endpoint.

Combining outcomes can provide a single measure of whether participants experienced at least one of several prespecified events. In this case, the composite brings mortality and qualifying bleeding into the same endpoint. It does not, by itself, show how much each component contributes to the overall result, and a change in the composite could reflect a change in one component, the other, or both. Component-specific primary results are not reported in the registry record.

The registry description states that a time-to-event analysis was used so participants could be included without requiring complete follow-up for the full 30 days. Participants lost to follow-up were to be included and censored at the time they were lost. In general, censoring allows information up to the last known follow-up time to contribute to a time-to-event analysis; it does not establish what happened after that time. The stated approach therefore addresses incomplete follow-up through the analysis framework, but the registry record does not report how many participants were censored or the detailed model used.

7. Results Posted in the Registry

• Intervention Arm: 31.5% (94/298) versus 34.2% (101/295) on control; risk difference -2.7 percentage points (95% CI -10.3 to 4.9), risk ratio 0.92 (0.73–1.16); unadjusted two-proportion z-test p = 0.485.

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.

Mean (SD) Percentage of Days With WHO Grade 2 Bleeding or Above, Per Participant.

• 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:
  • Intervention Arm: mean 3.10 versus 3.20 on control; difference -0.10 (95% CI -1.50 to 1.30), standardized effect d = -0.01; z-test p = 0.889.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention Arm and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With a Thrombotic Event From First Administration of Trial Treatment up to and Including 120 Days After the First Dose of Trial Treatment is Received (N)

• 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:
  • Intervention Arm: 2.7% (8/300) versus 1.7% (5/297) on control; risk difference 1.0 percentage points (95% CI -1.4 to 3.3), risk ratio 1.58 (0.52–4.79); unadjusted two-proportion z-test p = 0.411.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention Arm and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Developing Veno-occlusive Disease (VOD; Sinusoidal Obstructive Syndrome, SOS) Within 60 Days of First Administration of Trial Treatment.

• 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:
  • Intervention Arm: 1.0% (3/300) versus 0.7% (2/297) on control; risk difference 0.3 percentage points (95% CI -1.1 to 1.8), risk ratio 1.49 (0.25–8.82); unadjusted two-proportion z-test p = 0.662.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intervention Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the clinical picture beyond the primary composite. They address the amount and timing of bleeding, the highest bleeding grade, platelet and red cell transfusions, survival without transfusion, thrombotic events, and other outcomes. Together, these measures describe distinct aspects of bleeding burden, supportive care, and safety rather than repeating a single measure of the primary endpoint.

The available secondary results do not form a uniformly consistent pattern that would sharpen the primary comparison. For mean percentage of days with significant bleeding, the arm means are close relative to the reported variability, and the unadjusted comparison interval includes no difference. For thrombotic events and veno-occlusive disease, the event counts are small and the comparison intervals are broad. These results are best viewed as estimates with considerable uncertainty, not as decisive evidence for or against a difference.

Secondary outcomes relate to the primary result by adding detail, but they cannot explain the primary composite unless component-specific results are reported. The registry record does not report a breakdown of the primary endpoint into death and bleeding. Nor do the secondary results replace the primary endpoint's defined 30-day comparison; some have different definitions and observation periods.

There are multiple secondary outcomes, and the registry record does not report a strategy for controlling the chance of false-positive findings across them. When many outcomes are examined, some may appear notable by chance even if no underlying effect exists. Unadjusted secondary comparisons therefore carry less evidential weight than a prespecified primary analysis and should be interpreted as supportive or exploratory, particularly when no analysis details are reported. The registry record also lists no reported analysis entries for the secondary results described, limiting the ability to know which comparisons were planned and how they were tested.

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

• Mean (SD) Percentage of Days With WHO Grade 2 Bleeding or Above, Per Participant.
• Time to First Episode of Bleeding of WHO Grade 2 or Greater up to Study Day 30.
• Highest Grade of Bleeding a Patient Experiences up to Study Day 30.
• Number of Platelet Transfusions Per Patient up to Study Day 30.
• Number of Red Cell Transfusions Per Patient up to Study Day 30.
• Proportion of Patients Surviving at Least 30 Days Without a Platelet Transfusion.
• Proportion of Patients Surviving at Least 30 Days Without a Red Cell Transfusion.
• Number of Participants With a Thrombotic Event From First Administration of Trial Treatment up to and Including 120 Days After the First Dose of Trial Treatment is Received (N)

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical results are easiest to interpret by distinguishing the outcome measure, the comparison between arms, and the uncertainty around each estimate. General statistical explanations below describe those ideas; details of the trial's original statistical plan are included only where the registry record states them.

What the primary percentage represents

The primary outcome is a proportion: the percentage of participants with death or WHO Grade 2 or greater bleeding during the defined 30-day period. A proportion describes how common the event was within the reported arm population. It is not a rate per unit of time, even though the registry says a time-to-event analysis was used to estimate the outcome and handle incomplete follow-up.

The posted arm estimates are 31.7% for TXA and 34.2% for placebo. They describe the observed results under the trial's endpoint definition and analysis. They do not alone establish a causal difference; interpretation also depends on the randomized comparison, the analysis approach, and the uncertainty shown by the confidence intervals.

How to read a risk difference

A risk difference compares the event proportion in one arm with the event proportion in the other. A value of zero corresponds to equal proportions. Values on opposite sides of zero indicate opposite directions of the contrast, according to the order of subtraction used. The posted comparison is expressed as a risk difference, and its interval spans zero. This means the data are compatible with no difference as well as with differences in either direction over the interval's range.

A risk difference is an absolute contrast, rather than a relative one. It answers how far apart the observed proportions are on the percentage-point scale. Other measures, such as a risk ratio or odds ratio, describe relative contrasts and can tell a different part of the same statistical story. No single measure should be interpreted without its uncertainty and the outcome's clinical context.

Confidence intervals

A confidence interval expresses uncertainty around an estimate. In general, a 95% confidence interval is produced by a procedure that, under its assumptions, would cover the underlying value in 95% of repeated samples. It is not a guarantee that a particular interval contains the true value, nor does it give the probability that a fixed true value lies inside the reported interval.

For this endpoint, the arm-specific 95% confidence intervals are 26.6% to 37.4% and 29.0% to 40.0%. These ranges show that the data do not estimate each arm's event proportion with pinpoint precision. The interval for the contrast is also important: because it includes zero and values in both directions, the data do not precisely settle the direction or size of the difference.

What a p-value can and cannot say

The unadjusted p-value for the primary comparison is 0.485. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it is not a measure of the probability that a treatment effect exists.

The word “unadjusted” indicates that the reported value is not presented as corrected for a family of multiple comparisons. The registry record does not report a multiplicity adjustment plan for the outcome set. The p-value should therefore be read alongside the effect estimate and confidence interval, not as a standalone verdict. A value that does not indicate strong evidence against a null model does not prove equivalence or absence of an effect.

Time-to-event analysis and censoring

The registry description says the primary endpoint used a time-to-event analysis so that participants could be included without being followed for the entire 30 days. It also says participants lost to follow-up were included and censored when lost. In general, a time-to-event method uses both whether an event occurred and when it occurred, while censoring records that follow-up ended before an event was observed. A censored participant is not automatically counted as event-free for the remainder of the study.

These methods rely on assumptions about follow-up and censoring. If participants who are censored differ systematically in their subsequent event risk, the analysis may be affected. The registry record does not report the number or timing of censoring events, a detailed description of the estimator, or diagnostic assessments of the censoring assumptions.

Why variation matters for continuous outcomes

One secondary endpoint reports the mean percentage of days with WHO Grade 2 bleeding or above, together with a standard deviation. The mean describes the average observed burden; the standard deviation describes how dispersed individual results are around that average. In general, greater variability makes a mean contrast harder to estimate precisely for a given amount of data. The reported standard deviations are substantially larger than the difference between the posted arm means, and the comparison interval includes values on either side of no difference.

For event counts and proportions, sparse events can also produce substantial uncertainty. This is relevant to outcomes with small numbers of reported events: an observed difference in counts can be unstable, and a wide interval signals that the underlying contrast is not tightly estimated. General statistical interpretation must account for that uncertainty rather than focus only on which arm has the larger count.

Recalculation and analysis provenance

Some displayed comparisons may be simple unadjusted recalculations from posted arm-level summaries. Such calculations do not incorporate an adjusted model unless explicitly stated. The registry record does not report analyses for the secondary outcomes included in the available comparisons. No discrepancy is flagged for the posted comparison results, so there is no stated conflict requiring the sponsor's analysis to take precedence.

For any outcome, the statistical result is conditional on its definition, population, and method. The registry record does not report enough detail to reconstruct the full analysis plan, including all model choices, covariate adjustments, or sensitivity analyses. Those omissions limit how far the statistical results can be independently evaluated.

11. Confidence Intervals and Precision

Precision is about how narrowly an estimate identifies a range of values compatible with the data and analysis. The primary arm estimates have 95% confidence intervals of 26.6% to 37.4% for the intervention arm and 29.0% to 40.0% for the control arm. Both intervals cover a range of possible event proportions rather than a single exact value.

The intervals overlap, and the posted confidence interval for the difference extends across zero. In practical statistical terms, the observed results do not determine whether the underlying contrast favors the intervention, favors the control, or is close to no difference. The point estimates are useful summaries, but they should not be mistaken for precise estimates of the treatment contrast.

Precision depends on more than the total enrollment. It is affected by the number of participants contributing to a particular outcome, how often the outcome occurs, the amount of follow-up, and the analysis method. Here, the primary outcome results use 298 participants in the intervention arm and 295 in the control arm, rather than the overall enrollment count. The registry record describes censoring for loss to follow-up but does not report how many participants were censored, so the contribution of incomplete follow-up to precision cannot be assessed from the record.

Confidence intervals do not show the range of all individual outcomes, and they do not account for every possible source of bias or uncertainty. They quantify sampling uncertainty under the analysis assumptions. The posted intervals therefore support a cautious reading: the primary result is not a precise estimate of the direction and magnitude of the contrast, and it does not establish equivalence.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations based on the observed effect, not the trial's original design justification. The registry record's original sample-size assumptions are not reported. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect.

For ordinary two-arm comparisons in the planning illustrations, the figures are participants per arm. For time-to-event planning, the figures are total numbers of events, using the Schoenfeld approach. The unit matters: a total-event target is not a participant count, because participants may have different follow-up and not all will experience an event.

The 80% power column describes the planned sample size or event target that would give an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the assumptions were correct. The 90% column describes a higher chance of detection under those same conditions and therefore requires a larger target. Power is a property of a planned design for a specified effect, not a measure of whether the completed trial found an effect.

Each planning scenario uses a fraction of the observed effect. Planning for a smaller effect requires more participants per arm, or more total events for a time-to-event calculation, to achieve the same target power. This is not observed power: it is a set of prospective planning illustrations, and the observed effect may be a noisy estimate of the effect that a future study would seek to detect.

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 = 0.342; treatment proportion p₁ = 0.315; average p̄ = 0.329.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6644 = 1.3022.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6641 = 0.5590.
4. n = (1.3022 + 0.5590)² / (-0.0269)² = 4,774.2, rounded up to 4,775 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 <- 0.342372881355932                          # control proportion
p1 <- 0.315436241610738                          # 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(3136445)
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 = 4,775 (80% power), 6,391 (90% power)
 75% of observed effect: n per arm = 8,533 (80% power), 11,422 (90% power)
 50% of observed effect: n per arm = 19,296 (80% power), 25,831 (90% power)
power.prop.test: 4774.2 
Simulated power at n = 4,775 per arm: 0.800 (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

The registry record lists 18 outcome measures and 13 secondary outcomes posted. The primary endpoint is a defined composite, while the secondary outcomes cover several other clinical and supportive-care measures. With multiple outcomes, the chance of at least one apparently unusual result can increase if each is assessed separately. A multiplicity strategy may address this, for example by specifying which comparisons are confirmatory and whether significance thresholds are adjusted. Such a strategy is not reported in the registry record.

The posted secondary comparisons are described as unadjusted, and the registry record does not report secondary analysis entries. It is therefore not possible to determine from the record which analyses were prespecified, whether any were exploratory, or how the investigators intended to interpret the full family of outcomes. The secondary findings should not be treated as independent confirmations of the primary result.

For the primary endpoint, the registry description states that participants lost to follow-up were to be included and censored at the time they were lost. This is a stated approach for incomplete follow-up in a time-to-event analysis. The number of participants lost, the timing of losses, and the amount of missing primary-outcome information are not reported in the registry record. Missing-data handling for the secondary outcomes is also not reported in the registry record.

The primary population is described as participants with primary outcome data reported. The record does not provide a detailed analysis-population definition, a participant flow accounting for every randomized participant, or reasons for differences between enrollment and outcome denominators. It also does not report whether analyses were based on assignment as randomized or on treatment received. These details matter because analysis populations can affect interpretation of a randomized comparison.

The registry record does not report the original sample-size justification, interim analyses, stopping rules, or a complete statistical analysis plan. It is therefore not possible to assess whether the posted outcome set and comparisons reflect the full planned analysis or to evaluate all safeguards against selective reporting. These are limits of the information in the record, not evidence that a particular procedure was or was not used.

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: other saes (at least one event) (11.8%), sepsis (at least one event) (9.1%), fever (at least one event) (6.7%), gvhd (at least one event) (2.4%), organ failure (at least one event) (2.0%).

For serious adverse events, the registry reports 77 participants affected among 300 at risk in the intervention arm and 82 among 297 at risk in the control arm. For the separately listed other adverse-event category, it reports 8 among 300 and 5 among 297, respectively. Death counts are 23 and 14. These counts use the safety populations and should not be substituted for the primary outcome denominators.

The registry also lists serious adverse-event terms, including other SAEs, sepsis, fever, GvHD, organ failure, and transfusion reaction, with percentages attached to those terms. The record does not establish in the available description that these percentages are arm-specific, so they should not be assigned to one arm. Serious-event categories and individual event terms may also represent different ways of grouping the reports.

Counts alone do not quantify the precision of a treatment contrast. No confidence intervals or adjusted safety comparisons are reported in the registry record. Differences in the reported counts should therefore be read descriptively, without treating them as proof of a safety difference or its absence. The event definitions, severity grading details, and analyses underlying these safety summaries are not reported in the registry record.

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

The primary result describes the proportion of participants in each arm who experienced death or WHO Grade 2 or greater bleeding during the first 30 days, under the registry's stated outcome definition and analysis approach. The reported proportions were 31.7% in the intervention arm and 34.2% in the control arm. The confidence intervals and comparison indicate substantial uncertainty about the size and direction of the underlying contrast.

The result does not establish that the treatments are equivalent. A test that does not provide strong evidence against no difference is not the same as an equivalence test, and the registry record does not report an equivalence margin. Nor does the result establish a treatment benefit or harm. The comparison interval spans no difference and values in both directions, which means the posted estimates do not settle the question.

The composite endpoint also does not reveal which component drove the observed events. Death and qualifying bleeding are combined, and component-specific primary estimates are not reported in the registry record. The secondary outcomes provide additional information about bleeding, transfusions, thrombotic events, and other outcomes, but their multiplicity and analysis limitations make them insufficient to overturn or resolve the primary result.

Interpretation is specific to the participants enrolled, the intervention and placebo regimens, and the outcome and timeframe used. The registry record does not provide detailed demographic or clinical subgroup results, a full analysis plan, or complete missing-data accounting. The posted results therefore answer a defined randomized comparison but leave uncertainty about several further questions. They should be read as estimates with uncertainty, not as a universal conclusion about every patient group, regimen, or outcome.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be interpreted through both its estimate and its uncertainty. The two primary arm percentages differ as point estimates, but the confidence intervals around the arm estimates are broad, and the interval for the comparison spans no difference. Focusing only on which percentage is numerically lower would overstate what the data establish.

It also demonstrates the importance of distinguishing a composite endpoint from its components. The primary outcome combines death and WHO Grade 2 or greater bleeding, making it a single summary of either event within the specified period. Without component-specific results, the overall estimate cannot show whether the event pattern was driven by death, bleeding, or both. This is a general interpretive issue for composite outcomes.

The registry record further highlights the difference between trial results and planning assumptions. Sample-size illustrations based on observed effects can show how future planning changes when smaller effects are targeted, but they are not evidence that the completed trial had a particular probability of success. The original design justification is not reported in the registry record.

Finally, the number and variety of secondary outcomes make multiplicity and transparent analysis reporting important. Secondary outcomes may broaden understanding, but unadjusted comparisons without reported analysis details have limited confirmatory force. A careful reading keeps the primary result, its precision, secondary context, and limits of registry reporting distinct.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations arise from the registry information available for this trial. The primary endpoint combines death with bleeding of WHO Grade 2 or greater, and the record does not report separate primary estimates for those components. It also does not give detailed information on event adjudication or the operational procedures used to classify bleeding grades.

The primary outcome population is described as participants with data reported, while the enrollment and safety denominators differ from the primary denominators. The record does not provide a complete participant flow or reasons for those differences. Although the primary description says lost participants were censored at loss to follow-up, the number and timing of losses are not reported. Missing-data methods for secondary outcomes are also not reported.

The registry record lists numerous secondary outcomes but does not report a multiplicity plan or analysis entries for those results. This makes it difficult to distinguish confirmatory from exploratory comparisons or to assess how the full set of outcomes was handled. The original statistical analysis plan, sample-size justification, interim-analysis plans, and stopping rules are not reported in the registry record.

Some safety summaries are counts without comparative confidence intervals or adjusted analyses. The record also does not specify in the available description whether the listed serious adverse-event term percentages are arm-specific. In addition, detailed participant characteristics and subgroup results are not reported in the registry record. These gaps limit assessment of generalizability, subgroup patterns, and the robustness of the observed comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: TRial to EvaluAte Tranexamic Acid Therapy in Thrombocytopenia — NCT03136445.
• Registry record last updated 2025-10-28; status last verified 2025-09.
• Results first posted 2025-10-28.
• 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

NCT03136445 is a completed, phase 3 randomized, parallel-group study sponsored by NHS Blood and Transplant. It enrolled 616 participants and compared TXA with placebo in patients with haematological malignancies and severe thrombocytopenia. The registry records quadruple masking; the official title describes the study as double-blind.

The primary endpoint was death or WHO Grade 2 or greater bleeding during the first 30 days from first or planned first dose. Reported proportions were 31.7% in the intervention arm and 34.2% in the control arm, with 95% confidence intervals of 26.6% to 37.4% and 29.0% to 40.0%. The unadjusted p-value was 0.485, and the comparison interval spans no difference.

Secondary and safety results add context but have limitations, including uncertainty around sparse events and unreported multiplicity and analysis details. The registry record does not report the complete statistical plan, original sample-size justification, or detailed accounting of missing data.