Pragmatic Prehospital Group O Whole Blood Early Resuscitation Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pragmatic Prehospital Group O Whole Blood Early Resuscitation Trial (NCT03477006), a randomized phase 3 study. The primary outcome is 28 Day All Cause Mortality.

2. Clinical Question

The trial also recorded multiple organ failure and mortality within 24 hours from admission. Those outcomes provide additional descriptions of the trial results, but they do not replace the listed primary endpoint.

The question concerns a comparison between two care strategies beginning in the prehospital setting and continuing into early in-hospital care. The registry record describes random allocation and a parallel-group design. The posted results include the number of participants with each event in each group, along with comparisons between groups.

The clinical question is limited to these recorded outcomes and the enrolled trial population. The registry record does not report further details of eligibility criteria, the characteristics of participants at baseline, or the reason the trial was terminated. It also does not report the intended sample-size justification or the full analysis plan.

3. Trial Design

The PPOWER trial is listed as a Phase 3, randomized, single-masked, parallel-group interventional study. Its official title describes it as prospective and as a pilot clinical trial. The registry record reports 86 participants enrolled: 40 in the LTLR-WB group and 46 in the Standard Care group.

The intervention group received 2 units of low-titer, leucocyte-reduced, platelet-replete whole blood initiated during air medical transport. The description allows whole blood to continue up to 6 units, followed by standard component resuscitation, through the early in-hospital phase of care. The comparator group received standard prehospital air medical care and standard-of-care component trauma resuscitation described as 1:1:1 through that phase. The registry record does not identify who was masked.

The listed primary outcome is 28-day all-cause mortality, measured as the number of participants with the event, with the timeframe stated as 28 days from admission. The two posted secondary outcomes are incidence of multiple organ failure and 24-hour mortality. Their timeframes are 28 days and 24 hours from admission, respectively.

The registry record lists a start date of 2018-11-20, a primary completion date of 2020-10-30, and a status of terminated. The reason for termination is not reported in the registry record. The original sample-size target, its justification, the planned interim monitoring, and the full protocol-level statistical plan are also not reported in the registry record. The record therefore supports describing the randomized comparison and the results posted, but not reconstructing decisions or design assumptions that are absent.

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 28 Day All Cause Mortality, measured over 28 days from admission.

The primary endpoint is 28-day all-cause mortality, recorded as the number of participants who died from any cause within 28 days from admission. The posted results list 10 events among 40 participants in the LTLR-WB group and 12 among 46 participants in the Standard Care group.

All-cause mortality counts deaths regardless of their cause. In general, a mortality endpoint can provide a direct, clearly defined outcome for a clinical comparison, while avoiding the need to classify deaths by cause. That general property does not establish that the outcome is complete, free of measurement issues, or equally observed across groups; those details are not reported in the registry record.

The specified timeframe matters because the outcome is defined over a particular follow-up period. Deaths outside that period are not part of this endpoint as described. The registry record names the period as 28 days from admission, but does not report further details about follow-up procedures, missing outcome data, or how incomplete follow-up was handled.

The endpoint is reported as counts rather than as a time-to-event analysis. Accordingly, the posted comparison describes the proportion of participants with the event during the stated period, not the timing of deaths within that period. The endpoint alone does not describe other aspects of recovery or establish the effect of either care strategy on outcomes beyond the recorded measure.

7. Results Posted in the Registry

• LTLR-WB: 25.0% (10/40) versus 26.1% (12/46) on control; risk difference -1.1 percentage points (95% CI -19.6 to 17.4), risk ratio 0.96 (0.46–1.98); unadjusted two-proportion z-test p = 0.908.

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.

Incidence of Multiple Organ Failure

• 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:
  • LTLR-WB: 10.0% (4/40) versus 19.6% (9/46) on control; risk difference -9.6 percentage points (95% CI -24.3 to 5.2), risk ratio 0.51 (0.17–1.53); unadjusted two-proportion z-test p = 0.217.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LTLR-WB and the control. The interval gives the range of effects that remain compatible with the data.

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:
  • LTLR-WB: 15.0% (6/40) versus 17.4% (8/46) on control; risk difference -2.4 percentage points (95% CI -18.0 to 13.2), risk ratio 0.86 (0.33–2.28); unadjusted two-proportion z-test p = 0.764.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LTLR-WB and the control. The interval gives the range of effects that remain compatible with the data.

Across the two posted secondary outcomes, the point estimates are in the direction of fewer events in the LTLR-WB group. Both comparisons remain uncertain, with confidence intervals that include no difference. Their overall direction is consistent with the direction of the primary point estimate, but this pattern does not resolve the uncertainty in the primary result or establish a consistent effect across outcomes.

Multiple organ failure and 24-hour mortality are distinct outcomes with different timeframes and event definitions. They can add context to the primary result, but each addresses a separate question. The registry record lists these as secondary outcomes and does not report a hierarchy for interpreting them relative to one another or to the primary endpoint.

In general, testing multiple outcomes increases the opportunity for chance findings if each is interpreted as an independent confirmatory test. Whether or how that concern was handled in the trial is not reported in the registry record. Because multiplicity adjustment and a prespecified testing sequence are not reported, the secondary comparisons should be treated as exploratory or descriptive rather than as stand-alone confirmatory evidence. Their p-values should not be interpreted as though they were the only planned comparisons.

The secondary results should therefore be read as part of the total pattern of posted evidence, not as a way to overturn or replace the primary analysis. They do not remove the limitations created by the small enrolled sample and the uncertainty in the outcome comparisons. The registry record does not report additional secondary outcomes beyond the two posted.

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

• Incidence of Multiple Organ Failure
• 24 Hour Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: each participant either had the recorded event within the specified period or did not. For this outcome, the registry reports counts by group, and the recalculation expresses the comparison as a risk difference. The stated direction compares LTLR-WB with Standard Care, so a negative risk difference corresponds to a lower observed event risk in the LTLR-WB group. This is a general interpretation of the sign, not a claim about the cause of any observed difference.

What does the risk difference describe?

A risk difference subtracts one group’s event proportion from the other group’s event proportion. It is an absolute comparison on the probability scale, rather than a relative comparison. The recalculated primary risk difference is -0.011. Its confidence interval ranges from -0.196 to 0.174. The interval includes zero, the value corresponding to equal event risks under this measure. Because it also includes values on either side of zero, the data do not determine the direction of the underlying difference with precision.

The comparison also reports a risk ratio and an odds ratio. In general, a risk ratio compares event probabilities by division, while an odds ratio compares the odds of the event. These are relative measures and answer a different descriptive question from the absolute risk difference. For the primary outcome, the risk-ratio estimate is 0.958 with a confidence interval from 0.464 to 1.977; the odds-ratio estimate is 0.944 with a confidence interval from 0.357 to 2.497. Both intervals include the value corresponding to no relative difference. The registry record reports the sponsor’s Chi-squared p-value, but does not report the sponsor’s effect estimate or confidence interval.

How should the p-values be read?

The posted sponsor analysis uses a Chi-squared method and reports p = 0.91 for the primary comparison. The unadjusted recalculation from the posted counts gives p = 0.908. In general, a p-value measures how unusual results at least as incompatible with a specified null model would be if that model and the test assumptions held. It does not measure the probability that the null hypothesis is true, nor does it describe the size or clinical importance of a difference. A p-value alone also does not show the precision of the estimate, so it is read alongside the confidence interval and event counts.

The recalculated comparisons are unadjusted, simple comparisons of the posted group summaries. The registry record does not report covariate adjustment for the sponsor’s primary analysis, so no adjusted estimate should be inferred. The record also does not describe the exact calculation used for the recalculated confidence intervals. The reported sponsor method is identified as Chi-squared; additional details about its implementation are not reported in the registry record.

What does a confidence interval add?

In general, a confidence interval gives a range of estimates compatible with the data under the interval method and its assumptions. It conveys uncertainty around an estimate rather than identifying a single certain value. For the risk difference, zero is the no-difference value. The primary interval crosses zero and spans both negative and positive values, so it does not rule out either direction. The breadth of the interval also indicates that the observed sample does not constrain the possible difference closely. The interval should not be read as a guarantee that the true value lies within its endpoints.

Why does event frequency matter?

With binary outcomes, the amount of information depends in part on how many participants and events are observed. In general, estimates based on limited event counts tend to be less precise than estimates based on more information, all else being equal. The trial enrolled 86 participants and recorded 22 primary events across the two groups. That description does not by itself establish the adequacy of the design, because the registry record does not report the original target sample size, the assumptions used to plan it, or the intended detectable effect.

All-cause mortality is analyzed as a binary outcome over a fixed period in the posted comparison. Although the study title includes a 3 Year description, the primary endpoint’s stated timeframe is 28 days from admission. The registry does not report a time-to-event analysis for this endpoint. A time-to-event analysis would use event timing and follow-up information; those data and methods should not be presumed from a count-based result.

What can planning calculations tell readers?

In general, a power calculation estimates how many participants a hypothetical study would need under specified assumptions to have a chosen probability of detecting an effect at a chosen significance threshold. The planning illustration uses the observed effect as a starting point and considers stated fractions of it. Such calculations are sensitive to the effect size assumed: a smaller effect generally requires more participants to detect with the same power, assuming other inputs remain fixed. These illustrations do not show the probability that the completed trial detected an effect, and they do not establish the trial’s original design rationale.

The registry record’s planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These are assumptions for the planning illustration, not reported assumptions from the trial’s original design. The original design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.011, with a 95% confidence interval from -0.196 to 0.174. The range crosses zero and includes values representing differences in either direction. Thus, the estimate does not precisely distinguish a lower event risk in the LTLR-WB group from no difference or a higher event risk.

In general, a confidence interval describes the uncertainty of an estimate under the method used to construct it. It is not a range of outcomes for individual participants, and it is not a statement that the true value has a particular probability of being inside the displayed endpoints. A confidence interval is most informative when read together with the point estimate, its scale, and the study context.

The primary interval is wide relative to the central estimate, which indicates limited precision for the difference in event risks. The risk-ratio interval, 0.464 to 1.977, and odds-ratio interval, 0.357 to 2.497, also include their respective no-difference values. Those relative measures likewise leave substantial uncertainty about the magnitude and direction of the comparison.

Precision is not the same as statistical significance or clinical importance. A narrow interval could still include effects that matter to decision makers, while a result that meets a significance threshold would not by itself establish importance. The registry record does not report a threshold for clinical importance or a prespecified margin for equivalence or noninferiority. The posted intervals therefore support an uncertainty-focused interpretation, not a conclusion that the groups are equivalent.

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 figures are participants per arm, not total participants, because the outcomes in these calculations are binary participant counts. The registry record states that the planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It evaluates an effect equal to the stated fraction of the observed effect. The registry record’s original sample-size assumptions and justification are not reported.

The 80% power column means the hypothetical sample size per arm for a planning scenario intended to have 80% power under those assumptions. The 90% power column gives the corresponding per-arm size for a scenario intended to have 90% power. In general, power is the probability of detecting an effect of the assumed size under the specified model and threshold, if that effect and the assumptions hold. Neither column describes what happened in the completed trial.

The rows that use smaller fractions of the observed effect call for larger sample sizes. This follows the general relationship that smaller differences are harder to distinguish from random variation, so more participants are typically needed when other planning assumptions remain fixed. The observed effect itself is uncertain, especially in a small trial, and using it as the basis for a planning scenario does not make it a reliable prediction of an effect in future research.

The plotted curve is a visual way to follow the relationship between the assumed effect and the sample size required under the stated planning setup. The calculations are illustrations, not a reconstruction of the trial’s design process. This is not observed power.

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 = 0.261; treatment proportion p₁ = 0.250; average p̄ = 0.255.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6167 = 1.2088.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6167 = 0.5190.
4. n = (1.2088 + 0.5190)² / (-0.0109)² = 25,268.3, rounded up to 25,269 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 <- 0.260869565217391                          # control proportion
p1 <- 0.25                          # 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(3477006)
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 = 25,269 (80% power), 33,827 (90% power)
 75% of observed effect: n per arm = 45,079 (80% power), 60,348 (90% power)
 50% of observed effect: n per arm = 101,780 (80% power), 136,253 (90% power)
power.prop.test: 25268.3 
Simulated power at n = 25,269 per arm: 0.798 (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. Analyses Reported by the Sponsor

The sponsor’s posted primary analysis is a Chi-squared comparison with p = 0.91. The unadjusted recalculation from the posted counts gives p = 0.908. These values are close and are consistent at the displayed rounding level, while representing the registry analysis and the simple recalculation as distinct entries.

The recalculation additionally reports a risk difference of -0.011 with a 95% confidence interval from -0.196 to 0.174. The sponsor’s posted analysis entry does not report an effect estimate or confidence interval, so the recalculated estimate adds a descriptive measure of magnitude and uncertainty from the group summaries. It is not a substitute for a more detailed sponsor analysis or an adjusted estimate.

The registry record does not report enough detail to establish whether any other analysis choices differed between the sponsor’s analysis and the recalculation. The recalculated comparison is explicitly unadjusted. The sponsor’s reported result remains the trial’s own posted analysis, and the recalculation should be read as a complementary summary rather than as evidence that the sponsor’s analysis is incorrect.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and two secondary outcomes. It reports a sponsor analysis for each outcome, but does not report a multiplicity adjustment, a hierarchical testing sequence, or rules for prioritizing results if outcomes point in different directions. Whether such procedures were specified elsewhere is not reported in the registry record.

In general, examining multiple outcomes can increase the chance that at least one comparison appears unusual by chance. Adjustment methods or a prespecified testing hierarchy can help control how results are interpreted across a family of comparisons. Without reported details, it is not possible to determine whether the posted secondary p-values were intended to support confirmatory claims or how they should be interpreted under a broader testing plan.

The registry record does not report how missing outcome data were handled, whether all enrolled participants were included in every analysis, or how analysis populations were defined. It does not report an intention-to-treat, per-protocol, or other analysis population label for these results. The posted group counts and denominators do not, on their own, establish whether there were missing observations or how any were treated.

The record also does not report interim analyses, stopping rules, or whether any interim results informed termination. The trial status is terminated, but the reason and decision process are not reported in the registry record. These omissions limit assessment of whether the analyses followed a prespecified plan and whether the posted estimates could be affected by data availability or analysis choices.

In general, conclusions from a randomized comparison are easier to assess when outcome definitions, follow-up, missing-data handling, analysis populations, and multiplicity procedures are transparently described. The registry record provides endpoint labels, group results, and reported test methods, but does not include these additional details. Their absence should be treated as uncertainty about the analysis documentation, not as evidence that any particular procedure was or was not used.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ards (7.5%), stroke (6.5%), dvt (6.5%), rhabdomyolysis (4.3%), pulmonary embolus (2.5%).

The adverse-event record lists serious events affecting 7 of 40 participants in the LTLR-WB group and 11 of 46 participants in the Standard Care group. It lists other adverse events affecting 0 of 40 and 1 of 46 participants, respectively. The record also lists 10 and 12 deaths in the two groups. The death counts correspond to the posted primary endpoint counts, but the registry record does not explain whether these categories overlap in every detail.

The listed serious-event terms include ARDS at 7.5%, stroke at 6.5%, DVT at 6.5%, Rhabdomyolysis at 4.3%, pulmonary embolus at 2.5%, and gastrointestinal bleed at 2.2%. The registry record does not provide group-specific counts for these terms in the information posted, so they should not be attributed to one group or compared between groups on that basis.

These figures describe recorded events in the enrolled groups. They do not establish that an intervention caused or prevented an event, and the registry record does not report further detail about event severity classifications, ascertainment, timing, or causal assessment. The modest sample size also means that these counts should be read descriptively rather than as precise estimates of uncommon harms.

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

The results show that the registry recorded 10 participants with 28-day all-cause mortality among 40 in the LTLR-WB group and 12 among 46 in the Standard Care group. The unadjusted estimate of the risk difference is -0.011, and its confidence interval extends from -0.196 to 0.174. The interval includes no difference and values in both directions. The primary comparison therefore leaves substantial uncertainty about the direction and magnitude of a difference.

The results do not establish that the two care strategies are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin; such a margin is not reported in the registry record. Nor do the results establish that one strategy is superior. A p-value that does not indicate a clear difference is not proof that no difference exists.

The posted outcomes also do not establish the effect of either strategy on every aspect of patient health, on outcomes beyond the stated follow-up windows, or in populations not described by the enrolled trial. The trial record includes secondary outcome counts, but the associated uncertainty and unreported multiplicity procedures limit their confirmatory interpretation. Safety counts likewise describe recorded events and should not be treated as causal comparisons.

The trial was terminated, and the reason is not reported in the registry record. This status alone does not explain why the trial ended, whether it met its objectives, or whether the results were affected by a stopping decision. The registry record also does not report the original sample-size justification, missing-data approach, or analysis populations, so these cannot be used to strengthen or qualify the outcome interpretation beyond what is posted.

In general, a randomized trial can support a comparison within its enrolled population when allocation and follow-up are adequately implemented. The registry identifies randomization, but does not supply enough detail to assess all implementation and analysis features. The most defensible reading is therefore a descriptive one: the observed results and their uncertainty are reported, but they do not settle whether the strategies differ in 28-day mortality.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary result combines a point estimate with substantial uncertainty. A single estimate can look directional, but the confidence interval shows how much the data leave unresolved. Reporting the risk difference and interval alongside the group counts helps distinguish the observed comparison from a definitive conclusion about the underlying effect.

The trial also illustrates why a non-significant p-value should not be translated into evidence of equality. The primary p-values are not evidence that the groups are identical; the interval covers differences in both directions. The right interpretation is that this trial does not estimate the comparison precisely enough to determine a clear direction or magnitude.

Planning calculations based on an observed effect can help illustrate how assumed effect size relates to hypothetical sample requirements. They are not a record of the trial’s original planning, and the registry record does not report the original design assumptions. This distinction matters because retrospective planning illustrations cannot tell readers whether the trial was designed with a particular target effect or power.

The registry record also highlights the importance of transparent reporting beyond outcome counts. Multiplicity, missing-data handling, analysis populations, interim monitoring, and the reason for termination are not reported. These elements affect how readers assess the strength and scope of an analysis, and their absence constrains conclusions without proving that a particular method was omitted.

Finally, the secondary outcomes and adverse-event counts show why multiple endpoints require disciplined interpretation. They add context, but neither their direction nor their numerical presence substitutes for a prespecified analysis strategy. The statistical value of this record lies in making uncertainty and reporting limits visible, rather than in turning a small set of observed counts into a broad clinical claim.

19. Limitations

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

The trial enrolled 86 participants, and the primary outcome comparison is based on 22 recorded deaths across the groups. The confidence interval for the primary risk difference is wide and includes differences in either direction. The trial therefore provides limited precision for estimating the size and direction of the mortality comparison.

The registry record does not report participant baseline characteristics or detailed eligibility criteria. Those omissions limit assessment of how similar the randomized groups were in observed characteristics and how well the enrolled population can be described. The record identifies single masking but does not say who was masked or provide further information about allocation implementation.

The reason for the terminated status is not reported. The original sample-size target and its justification, interim monitoring, stopping rules, missing-data procedures, and analysis-population definitions are also not reported in the registry record. These gaps prevent assessment of whether the posted analyses followed a prespecified plan or how incomplete follow-up, if any, was addressed.

The posted sponsor analyses give p-values but do not provide sponsor effect estimates or confidence intervals. The recalculations offer unadjusted comparisons based on posted summary counts, but they cannot incorporate participant-level information or undocumented adjustments. Multiplicity procedures for the secondary outcomes are not reported, which limits their confirmatory interpretation.

Safety reporting is also limited: serious-event terms are listed with percentages, but group-specific term counts and further details about ascertainment or attribution are not reported. These limitations support a cautious interpretation of the posted results and do not establish that unreported procedures or information were absent from other records.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Pragmatic Prehospital Group O Whole Blood Early Resuscitation Trial — NCT03477006.
• Registry record last updated 2021-10-06; status last verified 2021-09.
• Results first posted 2021-10-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes the Pragmatic Prehospital Group O Whole Blood Early Resuscitation Trial as a Phase 3, randomized, single-masked, parallel-group interventional study in hemorrhagic shock. It lists 86 participants enrolled and a terminated status. The intervention was prehospital low-titer, leucocyte-reduced, platelet-replete whole blood continued into early in-hospital care; the comparator was standard prehospital and component trauma resuscitation.

The primary outcome was 28-day all-cause mortality. The posted counts were 10 of 40 in the LTLR-WB group and 12 of 46 in the Standard Care group. The unadjusted risk-difference estimate was -0.011, with a 95% confidence interval from -0.196 to 0.174. The sponsor-reported Chi-squared p-value was 0.91.

The record also posts multiple organ failure and 24-hour mortality, along with adverse-event information. The reason for termination, original sample-size assumptions, multiplicity procedures, missing-data handling, and analysis populations are not reported in the registry record. Overall, the posted primary comparison remains uncertain about the direction and magnitude of any difference.