Resuscitation Outcomes Consortium (ROC) Prehospital Resuscitation Using an Impedance Valve: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Resuscitation Outcomes Consortium (ROC) Prehospital Resuscitation Using an Impedance Valve (NCT00394706), a randomized phase 3 study. The primary outcome is Survival to Hospital Discharge With Satisfactory Function (Modified Rankin Scale [MRS] of Less Than or Equal to 3)..

2. Clinical Question

The trial asked whether two prehospital resuscitation strategies were associated with survival to hospital discharge with satisfactory function after non-traumatic cardiac arrest outside the hospital. One comparison tested an Impedance Threshold Device (ITD) against a sham device. The other tested early against later analysis of cardiac rhythm by emergency medical services providers. The study was designed as a factorial trial, so these interventions were evaluated as separate comparisons within the same trial.

The record describes a phase 3 randomized trial with triple masking and factorial allocation. Enrollment was 11738. The trial status is terminated. These design details identify the intended comparisons, but they do not by themselves establish that either strategy changed the outcome. The effect estimates and their uncertainty need to be considered alongside the endpoint definition and the reported analysis methods.

3. Trial Design

This was a phase 3, randomized, triple-masked, factorial study sponsored by the University of Washington. Its official title identifies both the impedance valve and the timing of rhythm analysis as study questions. Enrollment was 11738. The registry record lists the study start as 2007-06, primary completion as 2009-11, and status as terminated.

The factorial arrangement evaluated two intervention dimensions: an active ITD versus a sham ITD, and early versus later rhythm analysis. The early-analysis arm description says EMS providers assessed rhythm as soon as possible after arrival; approximately thirty seconds of CPR may have been performed before assessment. The later-analysis description specifies three minutes of CPR before rhythm assessment. The listed interventions were the ITD, sham ITD, analyze early, and analyze later.

The primary outcome was survival to hospital discharge with satisfactory function, defined using the Modified Rankin Scale (mRS). Secondary outcomes listed in the record include survival to hospital discharge, mRS at six months after discharge, an adult lifestyle and function version of the Mini-Mental Status Exam at six months, and Health Utilities Index III and Geriatric Depression Scale scores at six months. Four secondary endpoints have posted results.

The analysis populations were not identical across comparisons. The primary-outcome description says both intervention analyses excluded participants whose arrest was secondary to drowning, strangulation, or electrocution, or whose primary outcome was unknown. For the ITD-versus-sham comparison, it also describes exclusions involving device application and study eligibility, but the remaining text is incomplete in the registry record. Full eligibility criteria, the original sample-size justification, and the original statistical analysis plan are not reported in the registry record. The posted analysis methods are described separately below; they should not be mistaken for a complete protocol.

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.

Only the first 6 of 8 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analyses of both interventions excluded subjects who suffered arrest secondary to drowning, strangulation, or electrocution; or for whom the primary outcome was unknown. Additionally, the ITD vs. Sham analysis excluded subjects who did not have the device applied, had study exclusions, or who had a response time of more than 15 minutes.

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.

Only the first 6 of 9 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Survival to Hospital Discharge With Satisfactory Function (Modified Rankin Scale [MRS] of Less Than or Equal to 3)., measured over Hospital discharge or death prior to discharge.

The primary endpoint counted participants who survived to hospital discharge with satisfactory function. Satisfactory function was defined as an mRS score less than than or equal to 3 at discharge. The mRS is described in the registry record as a measure of the ability to function independently, with scores ranging from 0, no symptoms, to 6, death. The endpoint was binary: each participant either met the stated threshold at discharge or did not.

This combined endpoint captures more than survival alone. A participant needed to be alive at discharge and to meet the functional threshold. It therefore differs from the separately listed secondary endpoint of survival to hospital discharge, which does not incorporate the mRS threshold. The distinction matters when interpreting the results: a difference in survival alone would not necessarily imply a difference in survival with satisfactory function, and the reverse is also possible.

The endpoint timeframe was hospital discharge or death before discharge. The outcome description says that analyses excluded cases where the primary outcome was unknown, along with the specified arrest exclusions. The registry record does not report a detailed account of how unknown outcomes arose or how missing measurements were handled beyond those stated exclusions. The functional threshold makes the endpoint interpretable as a clinically meaningful category, but it also discards distinctions among scores within each side of the threshold. The reported binary event counts and risk differences should therefore be read as results for this specific combined definition, not as a summary of every aspect of survival or post-arrest function.

7. Results Posted in the Registry

• Analyze Early: 5.9% (310/5290) versus 6.0% (260/4345) on control; risk difference -0.1 percentage points (95% CI -1.1 to 0.8), risk ratio 0.98 (0.83–1.15); unadjusted two-proportion z-test p = 0.798.
• Analyze Later: 5.9% (273/4643) versus 6.0% (260/4345) on control; risk difference -0.1 percentage points (95% CI -1.1 to 0.9), risk ratio 0.98 (0.83–1.16); unadjusted two-proportion z-test p = 0.835.
• Active ITD: 5.8% (254/4373) versus 6.0% (260/4345) on control; risk difference -0.2 percentage points (95% CI -1.2 to 0.8), risk ratio 0.97 (0.82–1.15); unadjusted two-proportion z-test p = 0.728.

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.

Survival to Hospital Discharge

• 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:
  • Analyze Early: 8.1% (427/5290) versus 8.2% (355/4345) on control; risk difference -0.1 percentage points (95% CI -1.2 to 1.0), risk ratio 0.99 (0.86–1.13); unadjusted two-proportion z-test p = 0.860.
  • Analyze Later: 8.0% (372/4643) versus 8.2% (355/4345) on control; risk difference -0.2 percentage points (95% CI -1.3 to 1.0), risk ratio 0.98 (0.85–1.13); unadjusted two-proportion z-test p = 0.783.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Early and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Later and the control. The interval gives the range of effects that remain compatible with the data.

Modified Rankin Score at 6 Months After Hospital Discharge

• 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:
  • Analyze Early: mean 1.70 versus 1.60 on control; difference 0.10 (95% CI -0.20 to 0.40), standardized effect d = 0.06; z-test p = 0.514.
  • Analyze Later: mean 1.80 versus 1.60 on control; difference 0.20 (95% CI -0.11 to 0.51), standardized effect d = 0.11; z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Early and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Later and the control. The interval gives the range of effects that remain compatible with the data.

Adult Lifestyle and Function Version of Mini-Mental Status Exam at 6 Months

• 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:
  • Analyze Early: mean 18.30 versus 18.70 on control; difference -0.40 (95% CI -1.37 to 0.57), standardized effect d = -0.07; z-test p = 0.421.
  • Analyze Later: mean 18.50 versus 18.70 on control; difference -0.20 (95% CI -1.18 to 0.78), standardized effect d = -0.04; z-test p = 0.688.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Early and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Analyze Later and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the study beyond the primary combined measure. They include survival to hospital discharge and two measures assessed six months after discharge: mRS and the adult lifestyle and function version of the Mini-Mental Status Exam. Health Utilities Index III and Geriatric Depression Scale scores are also listed as secondary outcomes, although results are not posted for those measures among the four secondary endpoints with results.

Across the posted secondary results, there is no consistent pattern of clearly separated groups. The reported analyses and recalculated comparisons generally have confidence intervals that include the no-difference value. This broad pattern is compatible with the primary results, which also do not establish a clear difference. It does not mean that all outcomes are identical, nor does it establish that an effect on one outcome would necessarily appear on another: survival, a functional scale, and a cognitive or lifestyle measure represent different aspects of outcome.

Secondary outcomes commonly involve multiple comparisons. Each additional endpoint and contrast creates another opportunity for a nominally unusual result to occur by chance. Unless a multiplicity strategy is specified, isolated p-values from secondary analyses should carry less weight than a prespecified primary result. The registry record does not report a multiplicity adjustment, testing hierarchy, or a complete account of which secondary analyses were planned before the data were examined. The posted secondary estimates are therefore best viewed as exploratory or supportive context, rather than as definitive independent evidence.

Follow-up measures at six months also concern a subset with recorded assessment results, while the primary endpoint is assessed at discharge. The registry lists outcome-specific group counts, but does not fully describe follow-up completeness or missing-data handling for the secondary measures. This limits conclusions about whether the observed summaries represent all randomized participants. The overall secondary pattern is useful for understanding the range of outcomes assessed, but should not be used to overrule the primary result or to make a broad claim about every dimension of recovery.

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

• Survival to Hospital Discharge
• Modified Rankin Score at 6 Months After Hospital Discharge
• Adult Lifestyle and Function Version of Mini-Mental Status Exam at 6 Months
• Health Utilities Index III Score and Geriatric Depression Scale Score 6 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary, so the main effect measure is a risk difference: the event frequency in one group compared with the event frequency in its comparator, expressed as a subtraction on the risk scale. A risk difference of zero represents equal risks. A negative or positive value indicates direction only according to the order of groups used in the comparison, so the group labels must accompany the estimate. The sponsor’s reported values use the registry’s risk-difference presentation; recalculated values are unadjusted estimates from the posted counts.

What does randomization contribute?

Random allocation is intended to make comparison groups similar, on average, with respect to both measured and unmeasured characteristics at the start of a trial. That supports causal interpretation when the allocation is implemented as planned and the analysis preserves the randomized comparison. The registry lists randomized allocation, but the record does not report enough detail to assess allocation procedures, concealment, adherence, or every analysis-population decision. The documented exclusions are relevant because removing participants after randomization can affect how closely an analysis reflects the original randomized groups.

Why are there two intervention comparisons?

The factorial design evaluates the ITD-versus-sham question and the early-versus-later analysis question within one study framework. Each comparison has its own groups, estimate, and uncertainty. The group sizes shown for the separate comparisons should not be added together: the comparisons relate to different intervention dimensions and are not independent collections of participants. The record does not report a result for an interaction between the device and timing strategies, so no conclusion about whether their joint effects differed from what would be expected from the separate effects is warranted.

What do the sponsor methods say?

For the primary early-versus-later comparison, the registry reports a mixed models analysis of risk difference. For active ITD versus sham ITD, it reports a two-sided t-test for risk difference. The registry’s listed primary estimates are -0.2 and -0.1, respectively, with 95% confidence intervals and p-values. The posted secondary analyses use different methods: the survival comparison for timing is listed as generalized estimating equations (GEE), while the device survival comparison is listed as a two-sided t-test. The registry does not provide the full model specifications, covariates, correlation structure, or details of any robust variance estimation. Those elements are not reported in the registry record.

The recalculated risk differences use the event counts and group sizes shown for each comparison. They are unadjusted: they do not reproduce mixed models or other methods that may account for design features or covariates. For continuous outcomes, the recalculated mean differences compare posted group means, with confidence intervals based on the listed summaries. Such calculations are useful for orientation but can differ from a model-based result when the model uses additional information or a different analysis population.

Why can over-dispersion matter?

As a general statistical point, over-dispersion occurs when observed variation is greater than a model expects. For binary outcomes grouped in clusters or measured under correlated conditions, treating all observations as independent can understate uncertainty. Methods such as GEE or mixed models can account for some forms of correlation, depending on how they are specified. The registry names these methods for certain analyses, but it does not report enough detail to determine precisely how correlation or over-dispersion was handled in each model. No claim about a particular model adjustment can therefore be made from the method label alone.

How should p-values and intervals be read?

A p-value measures how unusual the observed data, or more extreme data, would be under a specified reference hypothesis and statistical model. It is not the probability that the null hypothesis is true and does not measure the probability that the result will replicate. A confidence interval represents a range of estimates compatible with the data and method at the stated confidence level, under repeated-sampling reasoning. When the interval crosses zero for a difference measure, the data do not clearly distinguish the estimate from no difference at the stated confidence level. That does not prove equality.

These concepts are general; the particular results depend on the registered endpoint definitions, analysis populations, and methods. The registry record does not report the original full statistical analysis plan, interim-analysis rules, or whether the final analyses followed a prespecified hierarchy. Those omissions limit assessment of how the reported tests fit into the full analysis strategy.

11. Confidence Intervals and Precision

For the primary endpoint, the sponsor-reported 95% confidence interval for early versus later rhythm analysis runs from -1.1 to 0.7 around a risk difference of -0.2. For active ITD versus sham ITD, the 95% interval runs from -1.1 to 0.8 around -0.1. Because each interval includes zero, neither result cleanly distinguishes a difference from no difference under the reported analysis. The intervals also include values on both sides of zero, so the direction is not determined with high precision.

Confidence intervals are useful because a point estimate alone can suggest more certainty than the data support. In general, an interval describes the uncertainty of an estimate under the specified method; it is not a guarantee that the true effect lies within that particular interval. The width reflects both the amount of information and variability, as well as analysis choices. In these results, the intervals are broad enough to leave room for effects in either direction within their bounds. They should not be read as proof that effects at the extremes are equally likely.

The unadjusted recalculations also have intervals spanning zero: -0.011 to 0.008 for early analysis, -0.011 to 0.009 for later analysis, and -0.012 to 0.008 for active ITD. These are recalculated on the risk-difference scale from posted group summaries and should be distinguished from the sponsor-reported estimates. The sponsor’s own analyses are the primary reported analyses; the recalculations are supplementary checks, not a replacement for them.

Precision is also limited by the analysis populations and outcome availability described in the record. The endpoint definition excludes cases with unknown primary outcomes, and the ITD comparison had additional exclusions. The registry does not fully describe missing-data handling or the implications of these exclusions. Thus, the intervals quantify statistical uncertainty for the analyzed data under their methods, not uncertainty arising from every possible source of bias or incomplete follow-up.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations derived from the observed effect, not the trial’s original design calculations. For these binary and continuous outcomes, the figures are participants per arm, not total events. In general, a per-arm figure describes the number of participants intended for each comparison group under the stated planning setup; it is not the combined number across groups.

The listed 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 a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record. The 80% power column describes the planned chance of detecting the chosen effect under the stated assumptions if that effect is the true one. The 90% power column uses a higher target chance of detection, which generally requires more participants under the same assumptions.

Within each outcome, the rows labeled as planning for 100%, 75%, or 50% of the observed effect show what happens when the assumed target effect is made smaller. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. This is a planning relationship, not evidence that the trial had a particular probability of finding an effect after its results were known. These figures are not observed power.

The illustrations use the recalculated observed effect as their starting point. Very small observed effects can therefore yield very large planning figures, and the values should not be treated as recommendations for a future study without considering its intended effect, population, analysis method, allocation, outcome, and feasibility. For time-to-event outcomes, the stated convention would be total events, but the posted outcomes described in these results are binary or continuous rather than time-to-event outcomes.

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 = 0.060; treatment proportion p₁ = 0.059; average p̄ = 0.059.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3338 = 0.6542.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3338 = 0.2809.
4. n = (0.6542 + 0.2809)² / (-0.0012)² = 570,847.0, rounded up to 570,847 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 <- 0.0598388952819333                          # control proportion
p1 <- 0.0586011342155009                          # 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(394706)
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 = 570,847 (80% power), 764,202 (90% power)
 75% of observed effect: n per arm = 1,017,325 (80% power), 1,361,908 (90% power)
 50% of observed effect: n per arm = 2,294,568 (80% power), 3,071,775 (90% power)
power.prop.test: 570847 
Simulated power at n = 570,847 per arm: 0.797 (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 registry reports the sponsor’s analyses alongside recalculations based on posted summary statistics. For the primary early-versus-later comparison, the sponsor reports a mixed models risk difference of -0.2, a 95% confidence interval from -1.1 to 0.7, and p = 0.59. For active ITD versus sham ITD, it reports a two-sided t-test risk difference of -0.1, a 95% confidence interval from -1.1 to 0.8, and p = 0.71.

The recalculated unadjusted risk differences are -0.001 for early analysis and -0.001 for later analysis, and -0.002 for active ITD. These use the posted counts and denominators, not the sponsor’s full model. Differences in scale or method mean the recalculations should not be treated as a direct replication of the registry’s analysis. The registry record does not supply full model specifications that would allow a complete reconstruction.

The posted primary estimates and recalculations share the broad statistical pattern of estimates near zero with uncertainty spanning zero. The record does not flag a discrepancy between the sponsor’s analyses and the recalculations. The sponsor’s own analyses remain the principal reported results; recalculated estimates are supplementary and unadjusted. Neither set of results establishes equivalence, and interpretation should give weight to the confidence intervals and the limitations of the reported analysis details, not only to p-values.

15. Multiplicity, Missing Data and Analysis Populations

The study asks more than one primary intervention question and lists several secondary outcomes. Repeated testing can increase the chance of at least one result appearing statistically notable even when there is no underlying effect. Statistical plans commonly address this through a prespecified hierarchy, family-wise error control, or another multiplicity strategy. The registry record does not report whether such a plan was used, how the two factorial comparisons were treated together, or whether secondary outcome testing was adjusted.

The primary comparisons should therefore be interpreted using their reported estimates and confidence intervals, while recognizing that the record does not document the full testing strategy. The secondary results deserve additional caution because multiple outcomes, contrasts, and timepoints can be considered. A nominal p-value, without an account of prespecification and multiplicity, is not enough to establish a confirmatory finding.

Missing data and analysis populations also affect interpretation. The primary outcome description states that cases with unknown outcomes were excluded, and it identifies exclusions for arrests secondary to drowning, strangulation, or electrocution. The ITD-versus-sham analysis has additional exclusions related to device application and study exclusions, but the population description is truncated. The registry does not report detailed missing-data reasons, imputation methods, sensitivity analyses, or whether the posted analyses follow intention-to-treat principles.

For the six-month secondary outcomes, group-specific result counts are listed, but the registry record does not give a complete account of follow-up completeness, loss to follow-up, or how missing measurements were handled. These omissions matter because an analysis of participants with observed follow-up can be biased if availability of measurements is related to outcome or intervention. The registry also does not report interim-analysis rules, stopping boundaries, or a full analysis plan. The trial status is terminated, but the reason for termination is not reported in the registry record. These gaps do not invalidate the posted estimates, but they limit independent evaluation of selection, analysis flexibility, and the strength of confirmatory claims.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: pulmonary edema (10.0%), airway bleeding (4.5%), liver lacerations (0.1%), defibrillator burns to chest (0.0%).

The registry lists serious adverse event counts for several analysis groups, including Analyze Early + ITD, Analyze Early + Sham, Analyze Later + ITD, and Analyze Later + Sham, as well as groups not included in particular comparisons. For example, the serious-event counts listed are 154 among 2310 for Analyze Early + ITD, 193 among 2321 for Analyze Early + Sham, 166 among 2156 for Analyze Later + ITD, and 174 among 2191 for Analyze Later + Sham. The entries for other adverse events list zero affected in the displayed groups.

The registry also identifies pulmonary edema at 10.0%, airway bleeding at 4.5%, liver lacerations at 0.1%, and defibrillator burns to chest at 0.0% among the top serious terms. These figures describe what is posted; the record does not give enough detail to establish how the terms were defined, whether the percentages use a common denominator, or how events were adjudicated. The group labels reflect the factorial comparisons and should not be combined by adding counts.

These summaries are not a complete safety assessment. The registry does not report deaths in the adverse-event summary, and the listed adverse-event figures alone do not establish a causal relationship to an intervention. They should be read as reported counts and terms, alongside the limitations in event definitions and analysis detail.

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

The posted results show estimates close to no difference for both primary intervention comparisons, with confidence intervals that include zero. The sponsor-reported early-versus-later estimate is -0.2, and the active-ITD-versus-sham estimate is -0.1. This means the registry analyses did not establish a clear difference in survival to hospital discharge with satisfactory function for either comparison. The results do not show that the interventions are equivalent, nor do they prove that no effect exists.

Failure to establish a difference is not the same as evidence that any possible difference is too small to matter. Equivalence or non-inferiority requires a prespecified acceptable margin and an analysis designed to assess that margin. No such margin or analysis is reported in the registry record. The confidence intervals describe statistical uncertainty under the reported analyses, but they do not resolve every uncertainty about study conduct, outcome completeness, or generalizability.

The primary endpoint combines survival and functional status at discharge. It should not be interpreted as a complete measure of long-term recovery. The registry includes secondary measures at six months, but their posted results also have uncertainty and incomplete documentation about missing follow-up and multiplicity. Those outcomes provide context rather than a basis for a broad claim about all aspects of recovery.

The trial record also describes exclusions from the primary analyses. The estimates apply to the analyzed populations and outcome definitions as reported, not automatically to every person experiencing out-of-hospital cardiac arrest. The findings should be understood as statistical results from this specific trial record, rather than as medical advice or a universal conclusion about treatment choices. The data support a cautious description: no clear difference was established in the primary endpoint, while the intervals and reporting gaps leave uncertainty.

18. Why This Trial Matters Statistically

Statistically, the trial is notable for evaluating two prehospital strategy questions within a randomized factorial design and using a binary primary endpoint that combines survival with a functional threshold. That structure makes the distinction between the two intervention contrasts important: timing of rhythm analysis and use of an active versus sham ITD are separate questions, each with its own estimate and uncertainty.

The results illustrate why a point estimate or p-value should not be read alone. The sponsor-reported primary estimates are near zero and their 95% confidence intervals cross zero, but that does not establish exact equality. The intervals preserve uncertainty in both directions, while the design and analysis details available in the registry determine how broadly the results can be interpreted.

The record also provides an opportunity to distinguish sponsor analyses from simple recalculations. Model-based results may reflect methods that cannot be reconstructed fully from summary counts. Unadjusted calculations can help readers orient to the direction and scale of estimates, but should not displace the sponsor’s analyses when the latter are reported and no discrepancy is flagged.

Finally, the trial demonstrates how outcome scope, analysis population, multiplicity, and missing follow-up affect interpretation even when the headline endpoint is clearly defined. The functional threshold is meaningful as a category but does not describe every degree of recovery. Exclusions and incomplete reporting of the statistical plan also constrain certainty. These considerations make transparent reporting of estimates, intervals, denominators, and methods essential to responsible statistical reading.

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.

Several limitations are specific to the available registry record. The primary-outcome population description is truncated, including the remaining criteria for the ITD-versus-sham comparison. The complete protocol, detailed eligibility criteria, and original sample-size justification are not reported in the registry record. The record also does not report why the study was terminated.

Although the registry names mixed models, GEE, and two-sided t-tests for selected analyses, it does not provide complete model specifications, covariate adjustments, or other details needed to reproduce the sponsor’s estimates. The original statistical analysis plan, interim-analysis procedures, and multiplicity strategy are not reported. Therefore, it is not possible to determine from the record alone how all comparisons were prespecified or how the family of tests was controlled.

The primary analysis excluded participants with unknown outcomes and specified arrest causes, while the ITD comparison had additional exclusions. Further detail about these exclusions and their timing is incomplete. The registry does not report sensitivity analyses that would show how alternative missing-data assumptions or analysis populations affect the results. For the six-month outcomes, posted group counts are available, but complete follow-up and missing-measurement handling are not described.

Safety information is also limited in the posted summary. Event definitions, adjudication procedures, and the meaning of some denominators are not fully documented, and deaths are not reported in the adverse-event summary. These limits do not negate the outcome estimates, but they restrict what can be concluded about robustness, generalizability, and safety from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Resuscitation Outcomes Consortium (ROC) Prehospital Resuscitation Using an Impedance Valve — NCT00394706.
• Registry record last updated 2018-08-09; status last verified 2018-07.
• Results first posted 2012-04-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT00394706 is a randomized, triple-masked, phase 3 factorial trial sponsored by the University of Washington. It evaluated an active ITD versus a sham ITD and early versus later cardiac-rhythm analysis during prehospital resuscitation for out-of-hospital cardiac arrest. Enrollment was 11738; the registry lists the study as terminated.

The primary endpoint was survival to hospital discharge with satisfactory function, defined as mRS less than or equal to 3. The sponsor-reported primary comparisons did not establish a clear difference: early versus later analysis had a risk difference of -0.2, with a 95% confidence interval from -1.1 to 0.7; active ITD versus sham had a risk difference of -0.1, with a 95% confidence interval from -1.1 to 0.8. The registry also reports secondary results, but does not report a complete multiplicity strategy, full analysis plan, or detailed missing-data handling. The estimates should be read with those reporting limitations in mind.