Analgesics in the Pre-hospital Setting: Implications on Hemorrhage Tolerance - Sufentanil: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Analgesics in the Pre-hospital Setting: Implications on Hemorrhage Tolerance - Sufentanil (NCT04959812), a randomized phase 1, phase 2 study. The primary outcome is Tolerance to Simulated Hemorrhage.

2. Clinical Question

The study’s stated purpose was to examine whether sufentanil alters responses to simulated blood loss. The laboratory procedure used lower-body negative pressure to create progressive central hypovolemia. Participants continued through the challenge until syncopal symptoms prompted test termination. Those symptoms were defined in the registry using a combination of physiological signs, including profound bradycardia and a marked drop in arterial blood pressure, and subjective symptoms such as light-headedness, sweating, nausea, or dizziness.

This is a physiological tolerance question under controlled research conditions. It is not a direct test of clinical outcomes after real hemorrhage, and the registry does not describe a patient population experiencing bleeding. The posted primary result compares means for the sufentanil and placebo limbs; it does not provide a separate estimate for each participant’s paired treatment response. Details of the planned primary hypothesis and the original analysis method are not reported in the registry record.

3. Trial Design

The registry identifies this as a randomized, single-masked, crossover study in Phase 1 and Phase 2. It lists the condition as healthy and enrollment as 46. The study record gives a start date of 2022-03-01, primary completion date of 2023-09-08, and status of completed. The sponsor is University of Texas Southwestern Medical Center.

The treatment conditions were sublingual sufentanil and sublingual placebo. The sufentanil intervention is described as a 30 microgram tablet. In a crossover study, treatment conditions are assessed within a participant according to the study design, rather than assigning every participant to just one treatment for the full comparison. However, the sequence, timing between treatment periods, and details of how the crossover was implemented are not reported in the registry record. The registry says masking was single but does not identify who was masked.

The primary outcome assessment took place over a timeframe listed as 6 hours. The registry describes a progressive lower-body negative pressure challenge and termination at onset of syncopal symptoms. The measured endpoint was a cumulative stress index based on the LBNP level multiplied by the duration at each level until termination. This operational definition gives the outcome a direct connection to the protocol’s laboratory challenge, while keeping it distinct from clinical hemorrhage outcomes.

The primary results report 29 observations for the sufentanil limb and 29 for the placebo limb. The registry’s enrollment figure and the number of observations reported for each limb do not, on their own, explain how many participants contributed paired data or how missing observations were handled. The analysis population, crossover sequence, and original sample-size rationale are not reported in the registry record. No inference about those design details should be made from the posted limb-level counts alone.

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 Tolerance to Simulated Hemorrhage, measured over 6 hours.

The primary endpoint is titled Tolerance to Simulated Hemorrhage and is reported as a mean in min*mmHg, with standard deviations. It quantifies the cumulative lower-body negative pressure exposure participants tolerated before the challenge was stopped for syncopal symptoms. The registry describes calculating the cumulative stress index by summing the product of each LBNP level and the time spent at that level. In practical terms, the measure combines the intensity and duration of the laboratory stress applied during the test.

This endpoint was used because the study’s question concerns physiological tolerance during simulated central hypovolemia. A higher cumulative index represents greater accumulated exposure to the protocol’s challenge before test termination; it does not itself measure blood loss, survival, or a clinical outcome after injury. The termination rule included physiological changes and subjective symptoms, so the measure depends both on the imposed challenge and on the criteria for ending it.

The registry lists the primary assessment timeframe as 6 hours. It does not report additional detail about the exact calculation applied to incomplete challenge stages, handling of missing endpoint values, or whether the primary analysis incorporated within-participant pairing. Those omissions limit how completely the reported group summaries can be connected to the full crossover design.

7. Results Posted in the Registry

• Sufentanil: mean 599.00 versus 651.00 on control; difference -52.00 (95% CI -231.48 to 127.48), standardized effect d = -0.15; z-test p = 0.570.

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.

Pain Assessment

• 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:
  • Sufentanil: mean 1.04 versus 1.16 on control; difference -0.12 (95% CI -0.33 to 0.09), standardized effect d = -0.29; z-test p = 0.271.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sufentanil and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is Pain Assessment. Its reported mean is lower in the sufentanil limb than in the placebo limb, and the posted unadjusted comparison has a p-value of 0.271. The registry reports the outcome over a 6 hours timeframe and in kg. These summaries describe a secondary measurement; they do not change the interpretation of the primary tolerance endpoint.

At a broad level, both the primary and secondary posted comparisons have point estimates below zero for sufentanil relative to placebo. This shared direction across the posted means is a descriptive pattern, not independent confirmation of a treatment effect. The endpoints measure different things, and one secondary comparison cannot validate or resolve the uncertainty around the primary comparison.

Secondary results generally carry less weight than the primary endpoint for confirmatory interpretation. They may be exploratory, may be among several outcomes or analyses considered, and can be more vulnerable to chance findings when multiplicity is not addressed. The registry record does not report a prespecified multiplicity strategy, hierarchy among outcomes, or analysis plan. The secondary p-value is unadjusted, so it should not be interpreted as though any adjustment for multiple testing had been applied.

The registry lists one secondary outcome and no reported analysis records. It is not possible to determine from the registry record whether additional analyses were planned, whether outcome reporting was complete, or how the secondary endpoint was intended to contribute to the study’s conclusions. The useful reading is therefore limited: the posted secondary summary adds context about another measured outcome, but does not provide a stronger basis for interpreting the primary result or establish a broader pattern beyond these reported measurements.

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

• Pain Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure summarized by its mean and standard deviation. A mean describes the average observed value in a group, while a standard deviation describes how dispersed individual values are around that group average. These summaries are useful for conveying the scale and variability of the outcome, but they do not show the full distribution or the individual trajectories through a crossover study.

What does the mean difference represent?

The reported mean difference is defined as the sufentanil result minus the placebo result. The estimate of -52.0 min*mmHg therefore represents a lower posted mean in the sufentanil limb than in the placebo limb. The estimate is a contrast between the two reported means, not a statement that every participant had a lower value under sufentanil. Group means can obscure considerable variation between participants and variation in treatment response.

In a crossover trial, each participant may contribute observations under both conditions. The statistical comparison can use the within-participant pairing, which is often informative because the same person’s outcomes may be more alike across treatment periods than outcomes from different people. To make that comparison, the analysis needs information about paired outcomes or the correlation between the two measurements. The registry record does not report the paired differences, that correlation, or the method used to account for pairing in the posted comparison. Separate limb means and standard deviations do not recover those details.

How should the confidence interval be read?

A confidence interval expresses uncertainty around an estimated contrast under the assumptions of the calculation. For the primary mean difference, the interval runs from -231.5 to 127.5 min*mmHg. It includes zero, which corresponds to no mean difference under this contrast, as well as values in either direction. It is therefore compatible with a range of possible mean differences, rather than pinpointing a single precise effect.

A confidence interval is not a range containing every individual participant’s outcome, and it does not mean that every value inside it is equally plausible. Its interpretation depends on the method and assumptions used to calculate it. The registry record does not report the confidence-interval method or whether it reflects the crossover structure. The posted interval can be described as reported, but the omitted details constrain further methodological evaluation.

What does the p-value add?

The primary unadjusted p-value is 0.57. In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be under that null model and the assumptions of the test. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. A large p-value does not establish equivalence or absence of an effect. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin; neither is reported in the registry record.

The p-value and confidence interval provide related information about the mean contrast, but neither removes uncertainty about the estimation method. The registry labels the comparison unadjusted, and the trial’s own statistical analysis plan is not reported in the registry record. The record does not specify the null hypothesis, test procedure, covariate adjustment, or handling of the crossover sequence. These omissions make it inappropriate to attribute an unreported statistical procedure to the study.

Why can dispersion matter?

Standard deviations describe variation in outcomes, while the standard error and confidence interval describe uncertainty in an estimated summary or contrast. General statistical reasoning distinguishes these quantities: a broad spread among participant outcomes can make a mean harder to estimate precisely, but the exact precision also depends on the analysis structure and the amount of usable information. In a crossover design, the relationship between outcomes from the same participant can affect precision. Without the paired data or correlation, the posted group standard deviations alone do not determine the uncertainty of a paired contrast.

General statistical methods also need to match the outcome’s distribution and design. If a continuous outcome has skewness or unusual values, mean-based methods can be sensitive to those features. The registry does not report distribution checks, robust methods, transformations, or sensitivity analyses. This is not evidence that such checks were omitted; their status is simply not reported in the registry record.

What is available for the secondary outcome?

The registry posts Pain Assessment as a secondary outcome, reported as a continuous mean with standard deviation. It also gives an unadjusted comparison and a p-value. The registry lists no reported analysis records. That does not erase the posted outcome summaries, but it means the details of the statistical procedures and any prespecified hierarchy cannot be established from the analysis records. Secondary findings are usually interpreted cautiously, especially when multiple outcomes or comparisons may be considered and no multiplicity plan is reported.

In general, multiplicity refers to the increased chance of finding an apparently notable result when many statistical tests are conducted. Adjustment procedures, a prespecified primary outcome hierarchy, or carefully limited confirmatory testing can address different aspects of this issue. The registry record does not report whether any such approach was used. The primary endpoint’s status as the listed primary outcome provides context, but it does not reveal the complete analysis plan.

The original sample-size justification, planned power, interim analyses, missing-data methods, and analysis populations are not reported in the registry record. The separate planning illustrations use the observed effect and stated assumptions; they are not evidence of the original design calculation. Statistical interpretation should therefore distinguish the posted estimates from details that the registry does not document.

11. Confidence Intervals and Precision

The primary mean difference is -52.0 min*mmHg, and its 95% confidence interval extends from -231.5 to 127.5. The interval crosses zero and is broad enough to include differences in either direction. This indicates limited precision for distinguishing the direction and magnitude of the mean contrast from the posted summary. The interval is more informative about uncertainty than the point estimate alone.

The point estimate is only one value among the range of estimates compatible with the confidence interval under its calculation. The negative estimate does not establish that the true contrast is negative, just as the positive values in the interval do not establish a positive contrast. The interval does not show the range of outcomes expected for individual participants. It concerns uncertainty about the estimated mean difference.

Precision depends on the information in the data and on the method used to estimate uncertainty. The reported standard deviations differ between the two limbs, and the study is described as a crossover. For a crossover comparison, the within-participant association can affect the precision of a treatment contrast. The registry record does not report the paired data, correlation, or confidence-interval method, so the posted interval cannot be independently evaluated as a paired estimate from the registry summaries alone.

The interval should not be read as proof of no effect or as evidence of equivalence. An equivalence conclusion would require a clinically justified margin and a design and analysis intended to assess that margin. Those details are not reported in the registry record. A nonsignificant p-value likewise does not resolve the uncertainty expressed by the interval.

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 for 80% power and participants per arm for 90% power. They are not total event counts. They are illustrations based on the observed effect, not the trial’s own original design calculation; the original design assumptions are not reported in the registry record.

The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. The row describing 100% of the observed effect uses that full observed estimate as the planning target; the rows describing 75% and 50% use progressively smaller target effects. Under the same planning framework, smaller effects require more participants to achieve the same target power.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect if that effect is the true one and the assumptions hold. The 90% power column gives the corresponding estimate for a 90% chance. Power is a property of a proposed design under assumptions; it is not the probability that the observed finding is true. These figures are not observed power.

The illustrations should not be treated as a recommendation for a future study or as evidence about the adequacy of this trial’s original enrollment. They rely on an observed effect, which can be uncertain, and on assumptions that may not match the crossover design or a future study. The registry does not report the original sample-size justification or planned analysis assumptions. The estimates therefore serve as conditional planning examples rather than a retrospective assessment of trial quality.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -52.000; pooled standard deviation σ = 348.701.
2. n = 2 × (1.96 + 0.842)² × 348.701² / -52.000² = 705.9, rounded up to 706 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
delta <- -52                      # observed difference in means
sigma <- 348.701161454905                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4959812)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 706 (80% power), 945 (90% power)
 75% of observed effect: n per arm = 1,255 (80% power), 1,680 (90% power)
 50% of observed effect: n per arm = 2,824 (80% power), 3,780 (90% power)
power.t.test: 706.9 
Simulated power at n = 706 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 investigators examine multiple endpoints, comparisons, time points, or analytic choices. Even when each test is conducted at a conventional significance threshold, considering multiple tests can increase the chance that at least one result appears notable by chance. Statistical plans can address this through prespecified outcome hierarchies, adjusted testing procedures, or clear distinctions between confirmatory and exploratory analyses.

The registry lists one primary outcome and one secondary outcome, and it reports no analysis records. The registry record does not report whether the study used a multiplicity adjustment, whether outcomes were tested in a hierarchy, or whether additional analyses were planned. The absence of a reported plan should be treated as missing documentation, not proof that no plan existed. The secondary result is unadjusted and should be interpreted with that limitation in mind.

Several other details relevant to interpreting the results are not reported in the registry record. These include the original statistical analysis plan, the definition of the analysis population, handling of missing outcome data, treatment of protocol deviations, and the method used to account for the crossover pairing. The sequence of treatment conditions and any period or carryover considerations are also not reported. These matters can affect how a crossover comparison is estimated and how broadly it applies to the participants included in the analysis.

The registry lists enrollment of 46, while the primary and secondary outcome summaries report 29 observations for each limb. The record does not explain the relationship between enrollment and those outcome counts. It does not state how many participants contributed complete paired data, why any enrolled participants may not appear in the outcome summaries, or whether the displayed counts refer to the same set of individuals in each condition. No totals or missing-data assumptions can be inferred from the limb-level counts alone.

Interim analyses, stopping rules beyond the described symptom-based termination of the laboratory challenge, and the original sample-size rationale are not reported in the registry record. As a result, the posted results can be described, but important elements needed to assess prespecification, analysis completeness, and missingness remain undocumented.

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.

The registry reports zero serious adverse events and zero deaths for both the sufentanil and placebo groups. It also reports zero other adverse events for both groups. The risk figures are listed for 29 in each treatment group. These are the adverse-event counts recorded in the registry; they should not be interpreted as evidence that no adverse events of any kind occurred outside the reporting framework.

Adverse-event counts depend on the definitions used, the observation period, ascertainment procedures, and the completeness of reporting. The registry record does not provide additional event terms for serious adverse events, and it does not report further detail about severity, timing, or how events were assessed. Zero recorded events therefore describes the posted safety summary rather than proving absence of risk.

The study involved healthy participants and a laboratory challenge, but the safety summary alone cannot establish safety in other populations or settings. It should be read alongside the study’s scope and the limitations of the registry reporting. These figures are descriptive and do not support medical advice.

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

The registry result describes a comparison of mean tolerance to a simulated hemorrhagic challenge under two treatment conditions in a study of healthy participants. The posted mean was lower in the sufentanil limb than the placebo limb, while the estimated difference was uncertain: its confidence interval includes zero and extends in both directions. The result does not precisely establish the direction or size of the mean contrast.

The finding is specific to a laboratory procedure using progressive lower-body negative pressure and a cumulative stress index. It is not a direct measurement of real blood loss, response to injury, or clinical outcome in people experiencing hemorrhage. The registry’s description supports interpretation of a physiological experiment, not extrapolation to emergency care or other populations.

A p-value of 0.57 does not demonstrate that the conditions have identical effects. Nor does the posted comparison establish that one treatment changes tolerance in a clinically meaningful way. The record does not report an equivalence margin or a minimal clinically important difference. Without such criteria, the clinical importance of a particular numerical difference cannot be assessed from the statistical comparison alone.

The crossover design raises an additional interpretive issue: paired data may be important to estimating the treatment contrast, but the registry does not report whether the comparison accounts for the within-participant relationship. The reported group summaries do not show participant-level changes. The original analysis plan and key missing-data details are also not reported, limiting evaluation of the robustness and completeness of the analysis.

The registry reports no serious adverse events, other adverse events, or deaths in either group. Those recorded counts are not proof of no risk and cannot be generalized beyond the reported study context. Taken together, the record offers a description of measured laboratory outcomes and their statistical uncertainty. It does not establish clinical benefit, lack of effect, equivalence, or safety in broader settings.

17. Why This Trial Matters Statistically

This study illustrates why an outcome’s definition matters to statistical interpretation. The primary measure combines the intensity and duration of a controlled laboratory challenge until symptom-based termination. It is a continuous cumulative measure, so means and standard deviations provide an accessible summary, but the endpoint remains a protocol-specific physiological quantity rather than a direct clinical outcome.

The crossover design also makes the structure of the data important. Participants may contribute results under both treatment conditions, and the within-participant association can influence the estimated contrast and its precision. The registry gives limb-level means and standard deviations, but does not report paired outcome data or whether the posted comparison used that pairing. This distinction matters because a design label alone does not reveal how the analysis was conducted.

Confidence intervals add useful context beyond a point estimate and p-value. The primary interval crosses zero and includes a broad range of values, making the uncertainty in the comparison visible. A nonsignificant result is not a demonstration of equivalence, and an observed point estimate should not be mistaken for a precise treatment effect. Clear reporting of analysis methods and intervals is therefore central to interpreting small experimental studies.

The record also demonstrates the difference between a trial’s original sample-size planning and a retrospective planning illustration based on an observed estimate. The registry does not report its original sample-size rationale. The posted planning calculations are conditional illustrations, not observed power and not evidence that the original design was based on those assumptions.

Finally, the limitations in registry reporting shape the conclusions that readers can responsibly draw. Details about pairing, missing data, multiplicity, and analysis populations are not reported. Recognizing these gaps is not a judgment about what investigators did; it is a boundary on what the public record establishes.

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 results come from a laboratory simulation of central hypovolemia in healthy participants. The registry record does not establish how the measured tolerance index relates to real-world hemorrhage or clinical outcomes. The endpoint is specific to the lower-body negative pressure protocol and its symptom-based stopping criteria, so generalization beyond that context is limited.

The study is described as crossover, but the registry does not report the treatment sequence, period details, washout interval, or handling of possible period or carryover effects. It also does not report whether the primary comparison accounts for paired measurements. This matters because the posted limb-level means and standard deviations do not reveal the within-participant differences that could be central to a crossover analysis.

The enrollment figure is 46, while each primary and secondary outcome limb is reported with 29 observations. The registry record does not explain the difference or describe the analysis population, completeness of paired observations, or missing-data handling. No conclusions about the reasons for the count discrepancy should be drawn from the available summaries.

The primary confidence interval is broad and includes zero, leaving substantial uncertainty about the mean contrast. Further methodological details—including the original analysis plan, distribution checks, covariate adjustments, and sensitivity analyses—are not reported in the registry record. The record also does not report the original sample-size justification or any multiplicity strategy. The secondary result is unadjusted and should be treated as less confirmatory than the primary outcome.

Safety findings are limited to the registry’s recorded event counts, with no additional serious-event terms or further detail on ascertainment. The absence of recorded events in these summaries does not establish absence of risk. These limitations concern the scope and documentation of the posted record; they do not establish that unreported procedures were or were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Analgesics in the Pre-hospital Setting: Implications on Hemorrhage Tolerance - Sufentanil — NCT04959812.
• Registry record last updated 2025-06-26; status last verified 2025-06.
• Results first posted 2024-07-11.
• 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

NCT04959812 is a completed randomized, single-masked crossover study sponsored by University of Texas Southwestern Medical Center. It is listed in Phase 1 and Phase 2 and enrolled healthy participants. The intervention was sublingual sufentanil, described as a 30 microgram tablet, compared with a sublingual placebo.

The primary outcome was tolerance to simulated hemorrhage, measured as a cumulative lower-body negative pressure stress index before onset of syncopal symptoms. The registry reports means and standard deviations for each treatment limb, along with an unadjusted mean-difference estimate and confidence interval. One secondary outcome, Pain Assessment, is also posted. The registry lists no reported analysis records.

The primary comparison is uncertain, with a confidence interval spanning zero. The posted results are specific to a laboratory challenge and should not be treated as evidence about clinical hemorrhage outcomes. Details about the original statistical plan, paired analysis, missing data, and multiplicity are not reported in the registry record.