Cold Stored Platelet in Hemorrhagic Shock: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cold Stored Platelet in Hemorrhagic Shock (NCT04667468), a randomized phase 2 study. The primary outcome is Study Feasibility.

2. Clinical Question

The trial record identifies a randomized, parallel-group comparison in patients with trauma and hemorrhage. Its intervention was an early platelet strategy, while the comparison arm received care according to each site’s standard practice. The primary question is about whether the trial procedures and follow-up could be carried out in the intended population; it is not itself a direct test of mortality benefit.

The posted feasibility outcome is expressed as participant counts: 91.0 of 102.0 in the CSP arm and 82.0 of 98.0 in the standard-care arm. The registry describes the underlying feasibility construct as the proportion of eligible patients who could be randomized, enrolled, adhere to protocol, and complete follow-up. It does not separately report the components, their individual counts, or a threshold defining successful feasibility. The difference between the posted counts therefore needs to be understood in light of that registry description, rather than as a fully detailed account of each feasibility component.

The clinical outcomes include mortality over several timeframes and other complications. The record identifies 24-hour mortality as the principal secondary clinical outcome, but the posted results do not include reported analyses. The comparisons can describe the observed counts and the registry’s listed estimates, while leaving uncertainty about the trial’s prespecified inferential approach and any conclusions drawn by investigators.

3. Trial Design

CriSP-HS is listed as a phase 2 randomized trial with a parallel-group design and single masking. The registry reports enrollment of 200 and a completed status. The recorded start date is 2022-06-21, and the primary completion date is 2023-10-07. The trial concerns trauma and hemorrhage.

The planned comparison was early infusion of urgent-release CSP versus standard care. The CSP arm description specifies early infusion of one apheresis unit. The standard-care arm description specifies resuscitation, blood transfusion, and blood-component transfusion according to site standard care. The record identifies Jason Sperry as sponsor.

The brief summary describes a proposed multicenter pilot trial using 5 level-1 trauma centers from within the LITES network and an approximate enrollment of 200 patients. That summary characterizes the proposed trial as open label, whereas the design field lists single masking. The identity of any masked participants or staff is not reported in the registry record, so the relationship between these descriptions cannot be resolved from the record alone.

The registry’s primary outcome is study feasibility, with a timeframe of enrollment through 30 days or discharge. Its description includes randomization, enrollment, protocol adherence, and follow-up completion. The listed secondary outcomes include 24-hour mortality, 3-hour mortality, in-hospital mortality, hemorrhagic death alone, acute respiratory distress syndrome, thromboembolic events, and 30-day mortality. Results are posted for the primary outcome and three mortality outcomes. The other listed secondary outcomes do not have posted results in the record.

Information about randomization procedures, allocation concealment, site-specific enrollment, and the identities of masked groups is not reported in the registry record. The original sample-size justification and the planned statistical analysis are also not reported. Although planning estimates can be illustrated from the observed results, those estimates are not evidence of the original design assumptions.

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

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 Study Feasibility, measured over Enrollment through 30 days or discharge.

The primary endpoint is titled study feasibility. The registry describes it as the proportion of eligible patients who can be randomized, enrolled, adhere to the protocol, and complete follow-up. Its stated timeframe runs from enrollment through 30 days or discharge. The posted outcome is represented as participant counts: 91.0 of 102.0 in the CSP arm and 82.0 of 98.0 in the standard-care arm.

A feasibility endpoint is used to assess whether the practical steps required for a larger or more definitive study can be carried out in the intended setting. It can address recruitment, delivery of the assigned intervention, adherence, and follow-up rather than serving as a direct measure of clinical benefit. For a pilot trial, those operational questions are especially relevant because a clinical outcome comparison may be imprecise even when the study procedures are workable.

The record does not give separate results for randomization, enrollment, protocol adherence, or follow-up completion. It also does not report a prespecified feasibility target or success threshold. Thus, the posted counts describe the registry’s primary outcome result, but do not show which component accounted for any participants who were not counted as meeting the combined description. The feasibility result should not be treated as a mortality finding or as proof of effectiveness.

7. Results Posted in the Registry

• Cold-stored Platelet (CSP): 89.2% (91/102) versus 83.7% (82/98) on control; risk difference 5.5 percentage points (95% CI -3.9 to 15.0), risk ratio 1.07 (0.95–1.19); unadjusted two-proportion z-test p = 0.252.

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.

24-hour 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:
  • Cold-stored Platelet (CSP): 5.9% (6/102) versus 10.2% (10/98) on control; risk difference -4.3 percentage points (95% CI -11.9 to 3.2), risk ratio 0.58 (0.22–1.53); unadjusted two-proportion z-test p = 0.260.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cold-stored Platelet (CSP) and the control. The interval gives the range of effects that remain compatible with the data.

3-hour 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:
  • Cold-stored Platelet (CSP): 5.9% (6/102) versus 7.1% (7/98) on control; risk difference -1.3 percentage points (95% CI -8.1 to 5.6), risk ratio 0.82 (0.29–2.36); unadjusted two-proportion z-test p = 0.718.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cold-stored Platelet (CSP) and the control. The interval gives the range of effects that remain compatible with the data.

In Hospital 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:
  • Cold-stored Platelet (CSP): 13.2% (12/91) versus 15.9% (13/82) on control; risk difference -2.7 percentage points (95% CI -13.2 to 7.9), risk ratio 0.83 (0.40–1.72); unadjusted two-proportion z-test p = 0.618.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cold-stored Platelet (CSP) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover mortality over three timeframes: 3-hour, 24-hour, and in-hospital mortality. Across these outcomes, the registry’s risk-difference point estimates are negative for CSP relative to standard care, but their confidence intervals include zero and extend to values on either side. The unadjusted comparisons therefore remain uncertain and do not establish a consistent, precise mortality difference.

The 24-hour outcome was identified in the brief summary as the principal secondary clinical outcome. It is separate from the primary feasibility endpoint: feasibility concerns whether participants could be randomized, enrolled, adhere to protocol, and complete follow-up, while mortality concerns clinical events. The feasibility result cannot answer the mortality question, and the mortality comparisons cannot establish whether trial procedures were feasible.

The record lists other secondary outcomes, including hemorrhagic death alone, acute respiratory distress syndrome, thromboembolic events, and 30-day mortality, but does not post results for them. The record therefore supports only a partial view of the planned secondary outcome set. It does not report analyses for the posted secondary outcomes, and does not give a multiplicity adjustment strategy.

Unadjusted secondary results generally carry less weight than a clearly prespecified primary analysis because repeated testing across multiple outcomes can increase the chance of apparently notable results arising by chance. This is a general statistical concern, not evidence that any particular finding is spurious. Here, the registry does not report a formal analysis plan or adjustment approach, so the secondary comparisons are best treated as descriptive and exploratory. Their estimates and uncertainty should be considered together, rather than selecting one result in isolation.

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

• 24-hour Mortality
• 3-hour Mortality
• In Hospital Mortality
• Hemorrhagic Death Alone
• Incidence of Acute Respiratory Distress Syndrome (ARDS)
• Incidence of Thromboembolic Events
• 30-day Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the study as randomized and parallel-group. Randomization is intended, in general, to make treatment assignment independent of participant characteristics, reducing the risk that systematic baseline differences explain an observed outcome contrast. A parallel-group design assigns participants to one of the compared approaches and follows each group. The registry does not report the precise randomization procedure, allocation concealment method, or any stratification factors, so those features cannot be described in more detail.

What does the risk difference describe?

For a binary outcome, a risk difference contrasts the proportion with the event in one group against the proportion in the comparator group. A positive value means the event proportion is higher in the CSP group under the displayed comparison direction; a negative value means it is lower. For feasibility, the event is the outcome counted as meeting the feasibility definition. For mortality, the event is death within the stated timeframe. The risk difference is expressed on the absolute proportion scale, which makes the direction and magnitude directly interpretable in the context of the event definition.

The posted estimates include confidence intervals. In general, a confidence interval describes the uncertainty around an estimated effect under the statistical method used to construct it. A wide interval indicates limited precision: a range of materially different effects can remain compatible with the data. If an interval for a risk difference includes zero, it includes the value corresponding to no difference on that scale. This does not prove that the true difference is zero; it indicates that the data do not distinguish zero from the other values within the interval at the interval’s stated confidence level.

How should the p-values be read?

The registry lists unadjusted p-values for the posted comparisons. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The registry does not report the test specification or a trial-wide analysis plan, so the listed values should not be assumed to represent adjusted, model-based, or otherwise prespecified analyses. A p-value needs to be read alongside the effect estimate, its interval, the outcome definition, and the design limitations.

The comparisons use group counts and denominators. The primary feasibility result uses 91.0 of 102.0 in the CSP group and 82.0 of 98.0 in standard care. The 24-hour and 3-hour mortality results use the randomized group denominators of 102.0 and 98.0. The in-hospital mortality result uses 91.0 and 82.0 as its arm denominators. The reasons for the different denominators in that outcome are not reported in the registry record. The record does not describe how missing or unavailable outcome data were handled, so differences in denominators should not be assigned an explanation without further information.

What is not known about the analysis?

No reported analyses are listed for the posted outcomes. The registry record does not report whether analyses followed intention-to-treat, per-protocol, or another population definition. It does not report covariate adjustment, handling of clustering by site, treatment of missing data, or methods for multiple comparisons. It also does not identify a primary statistical test or describe interim analyses. Those details affect how estimates and uncertainty are interpreted, and they cannot be inferred from the displayed summary statistics.

The trial is described in the brief summary as a pilot focused primarily on feasibility, with 24-hour mortality as the principal secondary clinical outcome. This distinction matters statistically. A feasibility study can inform whether recruitment and study procedures are workable, while a clinical endpoint comparison may have limited precision. The record does not report the original design assumptions or a sample-size justification, so the relationship between enrollment and a planned level of precision cannot be assessed from the registry record.

The record also posts ratios alongside risk differences. In general, a risk ratio compares event proportions by division, while an odds ratio compares event odds. These scales can express the same binary comparison differently, particularly when event frequencies vary. The risk-difference interpretation is used for the narrative because it is the metric identified in the posted comparison. No new estimates are derived from the ratios.

The planning illustrations are not analyses of observed trial power. They use stated assumptions for a hypothetical future design and the observed effect as a starting point. Such illustrations are sensitive to the effect size selected and to the assumptions used. They do not replace the original trial design rationale, which is not reported in the registry record. In general, a planning calculation estimates the enrollment needed to have a specified chance of detecting an effect under its assumptions; it does not establish that the current trial had that chance or that a nonsignificant result reflects absence of an effect.

11. Confidence Intervals and Precision

Precision is most clearly assessed from the confidence intervals around the risk differences. For feasibility, the estimate is 0.055 and its 95% confidence interval runs from -0.039 to 0.150. For 24-hour mortality, the estimate is -0.043 and its interval runs from -0.119 to 0.032. The 3-hour mortality estimate is -0.013, with an interval from -0.081 to 0.056. The in-hospital mortality estimate is -0.027, with an interval from -0.132 to 0.079.

Each interval spans zero, so each includes no difference on the risk-difference scale. The intervals also include values on either side of zero. This means the direction of the underlying difference is not settled by these estimates, and the data remain compatible with a range of effects. The clinical outcome intervals in particular do not support a precise estimate of the size of any difference. Their breadth should be considered alongside the relatively small group sizes and the low event counts reported for mortality.

In general, a confidence interval is not a guarantee that the true value lies within its endpoints. It is a measure of uncertainty generated under a statistical procedure and its assumptions. The registry does not report the procedure used to calculate these intervals, so the method cannot be evaluated from the record. The intervals are useful for seeing the range of estimates compatible with the posted summaries, but they do not resolve questions about missing data, analysis populations, or multiplicity.

The feasibility estimate also has uncertainty that matters for interpretation. Its point estimate is positive, but the interval includes zero and extends to both positive and negative values. Without a stated feasibility target and component-level results, the interval alone cannot establish whether the trial met a practical benchmark. Precision should therefore be understood as limited for both the feasibility contrast and the clinical comparisons, rather than reduced to whether an unadjusted p-value crosses a threshold.

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 express required enrollment as participants per arm for the binary outcomes in this trial. They are not totals across both arms and are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

For each listed effect scenario, the 80% power column means the planning calculation targets an 80% chance of detecting an effect of that size under the stated assumptions, if the assumed effect and model are appropriate. The 90% power column targets a higher chance of detection under those same assumptions and therefore generally requires more participants per arm. These are planning targets, not guarantees about a future study’s results.

The rows describe planning for 100%, 75%, and 50% of the observed effect. For example, the 24-hour mortality illustration gives 621 participants per arm for 80% power and 831 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 1,172 and 1,568; for 50%, they are 2,787 and 3,730. Smaller effects need more participants because they are harder to distinguish from random variation.

These numbers are not observed power. They are hypothetical planning illustrations based on the observed effect and the assumptions stated for the calculation. They do not show the power of the completed trial, and they do not establish what enrollment the investigators originally intended. The same caution applies to the other outcome-specific illustrations: their usefulness depends on whether the selected effect and planning assumptions are relevant to a future study.

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 = 0.837; treatment proportion p₁ = 0.892; average p̄ = 0.864.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4841 = 0.9488.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4825 = 0.4061.
4. n = (0.9488 + 0.4061)² / (0.0554)² = 597.7, rounded up to 598 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 <- 0.836734693877551                          # control proportion
p1 <- 0.892156862745098                          # 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(4667468)
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 = 598 (80% power), 800 (90% power)
 75% of observed effect: n per arm = 1,109 (80% power), 1,484 (90% power)
 50% of observed effect: n per arm = 2,597 (80% power), 3,476 (90% power)
power.prop.test: 597.7 
Simulated power at n = 598 per arm: 0.805 (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 evaluates multiple outcomes or performs multiple statistical tests. In general, the more comparisons made, the greater the chance that at least one result will appear unusual by chance if every comparison is judged independently. Prespecified priorities and an adjustment strategy can help clarify how a study intends to manage that issue. The registry record lists several secondary outcomes but does not report a multiplicity strategy, a testing hierarchy, or an adjusted analysis.

The record reports unadjusted p-values for the primary feasibility comparison and the posted mortality comparisons. No reported analyses are listed. It is therefore not possible to establish whether the displayed comparisons were specified in advance, whether additional analyses were conducted, or whether any correction was intended. The posted p-values should not be treated as family-wise adjusted evidence across the outcome set.

Missing-data methods and analysis populations are also not reported in the registry record. The record does not state how unavailable outcome information was handled, whether participants were analyzed according to random assignment, or whether adherence-based exclusions were applied. The in-hospital mortality denominators differ from the randomized group denominators, but the reason is not reported. Without these details, the effect of missingness or exclusions on the comparisons cannot be evaluated.

The record does not report whether analyses adjusted for baseline characteristics or study site, whether any interim analyses took place, or what model and inferential procedure were planned. These absences limit the ability to assess whether the posted estimates align with a prespecified analysis. They do not demonstrate that particular methods were or were not used outside what is recorded; they mean the relevant methods are not reported in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: thromboembolic events (5.9%), pneumonia (1.0%), coagulopathy (1.0%), transfusion associated cardiac overload (1.0%).

The registry lists serious adverse events affecting 9 of 102 participants in the CSP group and 4 of 98 in standard care. It lists zero other adverse events in each group. Death counts in the adverse-event record are 12 for CSP and 13 for standard care. These are reported counts and should be read with the group sizes and the registry’s definitions in mind.

The record lists thromboembolic events at 5.9%, and pneumonia, coagulopathy, and transfusion associated cardiac overload at 1.0% each among the leading serious adverse-event terms. It does not specify in this summary how those terms are distributed by arm or provide enough detail to infer causality. A recorded event after treatment is not, by itself, proof that the intervention caused it.

These adverse-event figures are descriptive. The registry does not provide a comparative safety analysis, event-level timing, severity grading beyond the serious-event classification, or detailed attribution. The counts should not be interpreted as establishing that either approach is safer. They indicate what the registry recorded, while leaving important context and comparative uncertainty unresolved.

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

The posted results describe a randomized comparison of early CSP infusion with standard care, with feasibility as the primary outcome and mortality as a key clinical outcome. The feasibility counts and risk-difference estimate provide information about the registry-defined operational outcome. The mortality counts and estimates describe observed events within the stated follow-up periods. Together, they offer a preliminary account of what was recorded in this completed phase 2 trial.

The estimates do not establish that CSP improves or worsens mortality. The confidence intervals for the posted risk differences include zero, and the record does not provide reported analyses beyond the unadjusted comparisons. The data are compatible with a range of possible differences. A point estimate favoring one arm should not be treated as a definitive treatment effect, especially when uncertainty is broad and the trial is described as a pilot focused primarily on feasibility.

Likewise, the primary feasibility result does not on its own establish that a larger study would be feasible. The record does not report a target threshold, separate component results, or detailed reasons why participants may not have met the combined feasibility description. A complete assessment would need those operational details as well as a clear account of the planned analysis.

The results also do not answer every outcome question in the registry. Several listed secondary outcomes have no posted results, and the multiplicity and missing-data approaches are not reported. Adverse-event counts are descriptive and do not establish causation or comparative safety. The registry record can be used to understand the posted observations and their uncertainty, but it is not a basis for medical advice or a definitive conclusion about the clinical value of either approach.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates feasibility from clinical effectiveness. In a pilot study, the practical ability to identify, randomize, treat, and follow participants is a central question. The registry makes feasibility the primary outcome and identifies 24-hour mortality as the principal secondary clinical outcome. Keeping those questions distinct helps avoid treating a successful operational result as evidence of clinical benefit, or treating an imprecise clinical comparison as a verdict on feasibility.

The study also illustrates why point estimates need uncertainty intervals. The mortality point estimates favor CSP in direction, but each posted interval includes zero and covers effects on both sides of no difference. A directional estimate alone can appear more conclusive than the data warrant. Reading the estimate together with its interval makes the uncertainty visible.

The planning illustrations show how assumptions about the effect size relate to the enrollment needed for a future study. In general, smaller target effects require larger samples to detect under otherwise similar assumptions. These illustrations can inform planning conversations, but they do not recover the original sample-size rationale, which is not reported, and they do not describe the completed trial’s observed power.

Finally, the record highlights the importance of complete statistical reporting. Details on analysis populations, missing data, multiplicity, and the treatment of site effects help readers understand how a randomized trial’s estimates were produced. Their absence does not invalidate the posted counts, but it limits independent assessment of the inferential conclusions. For biostatisticians and clinical researchers, that distinction between data description, analysis methods, and evidential strength is central to interpreting a pilot trial.

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.

The primary endpoint is described as a combined feasibility construct, but the registry does not report separate results for randomization, enrollment, adherence, or follow-up completion. It also does not give a threshold for judging whether feasibility criteria were met. This limits interpretation of the primary result as a practical go/no-go assessment.

The brief summary describes the proposed study as open label, while the registry design field lists single masking. The record does not identify who was masked, so the extent to which participants, clinicians, outcome assessors, or analysts were blinded cannot be determined. The allocation procedure and concealment details are also not reported.

The outcome denominators are not uniform across all posted results. The reason for the in-hospital mortality denominators of 91.0 and 82.0, rather than the randomized group sizes, is not reported. Missing-data handling and analysis-population definitions are absent. These gaps prevent assessment of whether the different denominators reflect follow-up availability, eligibility for a particular analysis, or another reason.

The registry lists seven secondary outcomes, but posts results for only three mortality outcomes. It does not report a multiplicity strategy or adjusted analyses. The posted comparisons are therefore limited in scope and are not a complete account of all listed secondary outcomes. The registry also does not report the original sample-size justification, interim analyses, or the planned statistical analysis.

Finally, the trial is described as a pilot, and the clinical outcome estimates have broad intervals. The results are informative as posted observations but do not provide precise estimates of mortality differences. These limitations are specific to the registry information available for this trial; additional protocol or analysis documentation is not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cold Stored Platelet in Hemorrhagic Shock — NCT04667468.
• Registry record last updated 2024-12-18; status last verified 2024-12.
• Results first posted 2024-12-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04667468, titled Cold Stored Platelet in Hemorrhagic Shock, is listed as a completed phase 2 randomized parallel-group trial. Enrollment is 200. The record gives a start date of 2022-06-21 and a primary completion date of 2023-10-07. It compares early infusion of one apheresis unit of urgent-release CSP with resuscitation and transfusion according to site standard care.

Study feasibility is the primary outcome, described as the ability to randomize and enroll eligible patients, maintain protocol adherence, and complete follow-up. The registry posts participant counts and a risk-difference estimate for this outcome. It also posts mortality results for 3-hour, 24-hour, and in-hospital timeframes. The listed confidence intervals for these comparisons include zero. Serious adverse-event counts and selected event terms are also recorded.

The brief summary identifies the study as a pilot and names 24-hour mortality as the principal secondary clinical outcome. No reported analyses are listed. The original statistical plan, sample-size justification, missing-data procedures, analysis populations, and multiplicity strategy are not reported in the registry record.