Low Dose Vasopressin in Traumatic Shock: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Low Dose Vasopressin in Traumatic Shock (NCT00420407), a randomized early/phase 1 study. The primary outcome is The Primary Endpoint of This Study Will be Day 30 Mortality..

2. Clinical Question

The study hypothesis concerned resuscitation approaches that limit total fluid volume while restoring organ perfusion. It proposed that such approaches could be associated with lower morbidity and mortality after trauma. That hypothesis is the rationale described in the registry; it is not itself a finding from the mortality comparison. The posted result addresses the recorded primary endpoint, not every aspect of resuscitation, organ perfusion, morbidity, or survival beyond the stated 30-day timeframe. The registry record does not report further details about the enrolled population, the treatment protocol, or how the primary comparison was adjusted, if at all.

3. Trial Design

The registry describes a prospective, randomized, double-blind, multi-center, parallel-group trial comparing low-dose vasopressin with placebo in traumatic-shock resuscitation. The masking field is recorded as triple masking. These design labels describe the planned allocation and masking framework, but the registry record does not identify which roles were masked or provide enough detail to reconstruct the allocation and concealment procedures.

The registered phase is early phase 1, and the study status is terminated. The registry lists enrollment as 81. For the primary endpoint, the posted arm counts are 37 for normal saline and 34 for vasopressin; the record does not explain how the enrollment figure relates to the arm counts contributing to this endpoint. It does not report the number screened, exclusions, withdrawals, crossovers, or the number included in a prespecified analysis population.

The study start is recorded as 2007-02 and primary completion as 2009-04. The registry identifies The University of Texas Health Science Center at San Antonio as the sponsor. It lists two outcome measures and one posted secondary outcome, “Level of Vasopressin After Trauma.” The registry records zero analyses. That entry should not be treated as proof that no analysis was conducted; it means the registry record does not post an analysis count or detailed statistical results under that field. The reason for termination, the original recruitment target, and any changes to the design or endpoints are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: clinical indication prohibiting potential use of vasopressin.

Overall Study

Reasons for not completing this period:

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.

Population: Vasopressin enrolled 40 and two withdrawn and never received drug (38) Normal saline enrolled 41 and one withdrawn and never received drug (40)

6. Primary Endpoint

The registry lists the primary outcome as The Primary Endpoint of This Study Will be Day 30 Mortality., measured over 30 days.

The primary endpoint is day 30 mortality, recorded as a number of participants. The registry description defines the measure in terms of survival after traumatic injury for at least 30 days after admission to the emergency room. The reported arm values are the numbers of participants with an endpoint event: 11 in the normal-saline arm and 13 in the vasopressin arm. The corresponding arm sizes for this endpoint are 37 and 34.

Mortality is a binary endpoint for each participant: the outcome is classified as an event or no event over the specified period. Summarizing the endpoint this way allows a direct comparison of the event risks between randomized groups. A fixed time horizon also makes the question explicit: the posted primary outcome concerns day 30, rather than mortality over an unspecified follow-up period. The registry does not report further details about how the endpoint was ascertained, how participants without complete follow-up were handled, or whether the analysis used any adjustment for baseline factors.

The endpoint is important to the stated study hypothesis, which concerns morbidity and mortality following trauma. However, the posted primary result only addresses the recorded day 30 mortality measure. It does not, by itself, describe other clinical outcomes or the mechanisms through which the treatments might affect resuscitation.

7. Results Posted in the Registry

• Vasopressin: 38.2% (13/34) versus 29.7% (11/37) on control; risk difference 8.5 percentage points (95% CI -13.5 to 30.5), risk ratio 1.29 (0.67–2.47); unadjusted two-proportion z-test p = 0.449.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: each participant is counted as having or not having the day 30 mortality event. General statistical explanation: for a binary outcome, a risk is the fraction of participants with the event among those counted in that arm. The registry reports 11 events among 37 participants in the normal-saline arm and 13 among 34 in the vasopressin arm. The arm-specific risks reported for the comparison are 0.297 and 0.382, respectively. These arm summaries provide the basis for the comparative measures.

What does a risk difference express?

A risk difference subtracts the comparator-arm risk from the intervention-arm risk. It expresses the absolute contrast in event risk using the same scale as the risks themselves. The posted risk difference is 0.085 for vasopressin relative to normal saline. A value of zero would represent equal risks; values above or below zero indicate which arm has the larger observed risk. The confidence interval runs from -0.135 to 0.305, so the reported estimate is compatible with both a negative and a positive difference. No new calculation is needed to interpret the interval: its position relative to zero is the key feature.

How do relative measures differ?

A risk ratio compares the event risk in one arm with the risk in the other. Its reference value for no relative difference is 1. The registry reports a risk ratio of 1.286 and a confidence interval from 0.669 to 2.474. An odds ratio compares event odds rather than event risks. Its reference value for no association is also 1. The posted odds ratio is 1.463, with a confidence interval from 0.545 to 3.928. Risk ratios and odds ratios have different interpretations and scales; neither should be read as an absolute risk difference. Their confidence intervals include their respective no-effect reference values, indicating that these estimates are also imprecise.

What does the p-value test?

General statistical explanation: a p-value describes how compatible the observed data are with a specified null hypothesis, under the statistical model and assumptions used for the test. The posted unadjusted p-value is 0.449. It is not the probability that the null hypothesis is true, nor does it measure the probability that a result will reproduce. A large p-value does not prove that the arms are equivalent, and a small p-value alone would not describe the clinical size or precision of an effect. The registry record does not report a detailed test specification or adjusted analysis.

Why does the confidence interval matter?

General statistical explanation: a confidence interval describes a range of effect estimates compatible with the data under a particular method, and reflects sampling uncertainty. A wider interval indicates less precision than a narrower interval on the same scale. Here, the risk-difference interval crosses zero and covers values in both directions. The relative-measure intervals also cross their no-effect value of 1. The intervals make clear why the point estimates should not be treated as conclusive evidence about the direction or magnitude of an effect.

What can be said about the analysis framework?

The registry identifies the trial as randomized and parallel-group, which means participants were assigned to one of two groups and outcomes are compared between those groups. The reported primary outcome is a participant count, and the comparison is presented using binary-outcome measures. The record does not report whether the analysis followed an intention-to-treat principle, how any departures from assigned treatment were addressed, whether baseline adjustment was used, or what method produced the interval estimates and p-value. It also does not report a detailed statistical analysis plan, interim analyses, or a sample-size justification. These details should not be inferred from the outcome summaries.

Why can a simple binary-outcome model be uncertain?

General statistical explanation: precision depends on the amount of information in the observed data, including the number of participants and events, as well as the variability of the outcome. With limited event information, estimates can vary substantially across samples, which is reflected in wider confidence intervals. Randomization supports a fair comparison in expectation, but it does not guarantee that a particular sample will yield a precise estimate. The posted endpoint counts and intervals illustrate this distinction: a randomized design can still produce uncertain estimates.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.085, with a confidence interval from -0.135 to 0.305. The interval spans zero, so the data are compatible with no absolute difference as well as with differences in either direction. The point estimate is not a precise stand-alone description of the treatment contrast: the interval permits a broad range of possible values.

The risk ratio is 1.286, with a confidence interval from 0.669 to 2.474. The odds ratio is 1.463, with a confidence interval from 0.545 to 3.928. Both relative-effect intervals include 1, the no-relative-difference reference value. Because the risk difference, risk ratio, and odds ratio use different scales, their numerical values should not be compared as if they were interchangeable. They consistently show uncertainty, rather than providing a narrow estimate of the contrast.

General statistical explanation: confidence intervals are useful because they show the uncertainty around an estimate, not just its central value. A confidence interval is not a guarantee that the true effect lies within its particular endpoints. Its interpretation depends on the method and assumptions used to construct it. The registry record does not identify the precise interval method or report enough information to assess all its assumptions.

The posted arm counts are 11 events among 37 participants for normal saline and 13 among 34 for vasopressin. The registry enrollment field is 81, while the outcome-specific arm counts are different in their presentation; the record does not explain the relationship between these figures. The precision of the comparison should be judged from the outcome-specific information and the reported intervals, not from the enrollment field alone. The record does not report missing-outcome counts or describe whether incomplete follow-up contributed to the endpoint denominators.

11. 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 events. They are illustrations based on the observed effect, rather than the trial’s original recruitment target. The trial’s own design assumptions and sample-size justification are not reported in the registry record.

The stated 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 figures for 80% power indicate the number of participants per arm required, under those assumptions, for a design to have an 80% chance of detecting the specified effect if that effect is real. The 90% power column uses the same planning idea but sets a higher probability of detection, which requires more participants per arm for a given effect.

For planning at 100% of the observed effect, the figures are 486 participants per arm for 80% power and 650 participants per arm for 90% power. For planning at 75% of the observed effect, they are 851 and 1,139 participants per arm. For planning at 50% of the observed effect, they are 1,883 and 2,521 participants per arm. The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation and therefore require more participants. These are planning illustrations, not observed power for the completed trial.

The figures depend on the assumptions stated for the illustration and on treating the observed effect as a reference for future planning. They do not demonstrate that a future study would obtain the same effect, nor do they replace a protocol-specific design calculation. The registry record does not report whether the trial’s original design used these assumptions or any other sample-size procedure.

12. 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 = 0.297; treatment proportion p₁ = 0.382; average p̄ = 0.340.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6698 = 1.3129.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6671 = 0.5615.
4. n = (1.3129 + 0.5615)² / (0.0851)² = 485.6, rounded up to 486 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 <- 0.297297297297297                          # control proportion
p1 <- 0.382352941176471                          # 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(420407)
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 = 486 (80% power), 650 (90% power)
 75% of observed effect: n per arm = 851 (80% power), 1,139 (90% power)
 50% of observed effect: n per arm = 1,883 (80% power), 2,521 (90% power)
power.prop.test: 485.6 
Simulated power at n = 486 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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists two outcome measures and one posted secondary outcome, “Level of Vasopressin After Trauma.” It records zero analyses. This does not establish that the investigators conducted no analyses; it indicates that the registry record does not report an analysis count or detailed analysis results under that entry. No secondary-outcome estimate or inferential result is posted in the information available for this account.

The record does not report whether the primary endpoint was prespecified in a statistical analysis plan, whether outcome definitions or analysis methods changed, or whether interim analyses were conducted. It also does not report a multiplicity strategy for accounting for tests across outcomes or analyses. Without that information, the extent to which the unadjusted p-value reflects a single planned comparison or a larger set of examined comparisons cannot be assessed. The p-value should be read as the posted unadjusted result, not as evidence that multiplicity was addressed.

Missing-data handling and analysis populations are also not reported in the registry record. In particular, the record does not state whether the primary comparison included all randomized participants, only participants with an observed endpoint, or another defined population. It does not describe imputation, censoring, withdrawal, or loss-to-follow-up procedures. The enrollment field is 81, while the arm counts attached to the primary endpoint are 37 and 34; no explanation of the relationship among these figures is reported. It would be inappropriate to infer a reason for that presentation or assume how unreported participants were handled.

These omissions limit a full assessment of analysis choices and potential bias. They do not change the arithmetic of the posted estimates, but they matter when judging whether the reported comparison follows the intended analysis and how completely it represents the randomized groups.

14. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: multiple organ failure (10.0%), traumatic brain injury (tbi) (10.0%), cardiopulmonary arrest (9.8%), pneumonia (9.8%), hemorrhagic shock (7.5%).

The serious-adverse-event entries list 41 participants at risk in the normal-saline group and 40 in the vasopressin group. The corresponding numbers affected by serious adverse events are 19 and 20. For other adverse events, the listed at-risk counts are 41 and 40, and the affected counts are 37 and 35. These safety entries are separate from the primary day 30 mortality comparison and should not be combined with its endpoint counts.

The registry also lists serious-event terms and percentages: Multiple Organ Failure, 10.0%; Traumatic Brain Injury (TBI), 10.0%; Cardiopulmonary Arrest, 9.8%; Pneumonia, 9.8%; Hemorrhagic Shock, 7.5%; and Deep Vein Thrombosis, 7.5%. These entries identify reported terms and their posted percentages; the registry record does not provide enough detail to determine the precise denominator or attribution for each term. The percentages should not be treated as proof that an event was caused by a particular intervention.

Deaths are not reported in the adverse-event group fields. The registry does not describe event severity definitions, timing, relatedness assessment, or whether participants could contribute more than one event. The figures therefore describe the safety entries as recorded, without establishing comparative safety or a causal relationship.

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

The result means that the registry posts a day 30 mortality comparison between the normal-saline and vasopressin groups, with 11 events among 37 participants and 13 among 34, respectively. The estimated risk difference is 0.085 for vasopressin relative to normal saline. Its confidence interval, from -0.135 to 0.305, includes no difference and values in both directions. The unadjusted p-value is 0.449. Together, these figures describe an uncertain estimate rather than a precise demonstration of a difference.

The result does not establish that vasopressin increases or decreases mortality, and it does not establish that the two groups have equivalent outcomes. Failure to distinguish a difference in this comparison is not the same as demonstrating equivalence or non-inferiority; the registry record does not report an equivalence or non-inferiority framework. The relative estimates are also uncertain, with confidence intervals that include the no-relative-difference value.

The trial’s hypothesis related to fluid volume, organ perfusion, morbidity, and mortality after trauma. The posted primary result does not answer every part of that hypothesis. It does not, by itself, report the effect on total resuscitation-fluid volume, organ perfusion, or all morbidity outcomes. The secondary outcome listed in the registry is Level of Vasopressin After Trauma, but no result for it is posted in the information. The record does not report enough detail to assess whether the termination status affected recruitment or outcome follow-up.

These findings should be understood as the estimates recorded for this trial, with the accompanying uncertainty and reporting limitations. They are not medical advice and do not determine what treatment should be used in an individual situation. A reader should not generalize beyond the study population, treatment comparison, and day 30 endpoint described in the registry. Eligibility details and the full analysis population are not reported in the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison and a statistically conclusive result are not the same thing. Random assignment is a design feature intended to support a fair comparison between groups. Yet the reported primary endpoint counts are limited, and the confidence interval for the risk difference extends across zero and into both directions. A trial can therefore be randomized and still leave substantial uncertainty about the size and direction of an effect.

The result also demonstrates the value of presenting more than a p-value. The unadjusted p-value is 0.449, but the risk-difference estimate and its interval show the range of effects compatible with the posted data. The risk ratio and odds ratio offer other scales for describing the contrast, and their intervals likewise include their no-effect references. These measures help distinguish an absence of strong evidence against a null hypothesis from evidence that two interventions are equivalent.

There is also a practical planning lesson. The illustrative participant requirements increase as the target effect becomes smaller and as the desired power increases. Those figures are based on the observed effect and stated planning assumptions, not on the trial’s documented original design. They show why sample-size planning depends on choosing a clinically relevant effect before a study begins, rather than treating the observed result as a guaranteed future effect.

Finally, registry completeness affects statistical interpretation. The record posts a termination status, primary endpoint counts, and adverse-event summaries, but does not report reasons for termination, missing-data procedures, analysis populations, or a detailed analysis plan. Such information is important for understanding how a result was generated and how far it can be generalized. The posted evidence should be interpreted in light of both its numerical uncertainty and the limits of what the registry record documents.

17. Limitations

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

Several trial-specific limitations are apparent from the registry record. The study status is terminated, but the reason for termination is not reported. The record lists enrollment as 81, while the primary outcome is reported with arm sizes of 37 and 34; the relationship between those figures is not explained. No information is reported about eligibility criteria, baseline participant characteristics, recruitment, treatment adherence, crossovers, withdrawals, or completeness of follow-up.

The registry does not report the vasopressin dose or detailed timing and administration procedures for the intervention. Although the trial is described as triple-masked, the roles masked and the procedures for maintaining masking are not reported. The record also does not specify the methods for endpoint ascertainment or whether the primary analysis adjusted for baseline variables.

The analysis population, missing-data approach, and statistical analysis plan are not reported. The registry does not state whether the primary comparison used an intention-to-treat approach, how participants with missing endpoint data were handled, or whether the analysis was prespecified. It also does not report any interim analyses or the trial’s original sample-size rationale. The number of registered outcome measures and the single posted secondary outcome do not, on their own, establish how many analyses were performed or whether multiple testing was addressed.

Finally, the primary comparison is imprecise: the risk-difference confidence interval includes zero and spans values on both sides of it. The posted findings therefore do not provide a narrow estimate of the treatment contrast. These limitations constrain interpretation of the posted results and should not be filled in with assumptions about the protocol or conduct.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Low Dose Vasopressin in Traumatic Shock — NCT00420407.
• Registry record last updated 2019-06-18; status last verified 2013-04.
• Results first posted 2013-04-16.
• 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.

21. Record Summary

The registry record describes a prospective, randomized, triple-masked, parallel-group trial of vasopressin versus normal saline during resuscitation for traumatic shock. The listed phase is early phase 1, enrollment is 81, and status is terminated. The recorded study start is 2007-02 and primary completion is 2009-04.

The primary endpoint is day 30 mortality. The registry reports 11 events among 37 participants assigned to normal saline and 13 among 34 assigned to vasopressin. The risk difference is 0.085, with a confidence interval from -0.135 to 0.305 and an unadjusted p-value of 0.449. Relative estimates are also imprecise.

The record lists one secondary outcome, Level of Vasopressin After Trauma, and posts serious and other adverse-event summaries. Reasons for termination, the original sample-size justification, analysis populations, missing-data handling, and a detailed statistical analysis plan are not reported in the registry record.