A Comparative Study Between a Pre-hospital and an In-hospital Circulatory Support Strategy (ECMO) in Refractory Cardiac Arrest (APACAR2): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparative Study Between a Pre-hospital and an In-hospital Circulatory Support Strategy (ECMO) in Refractory Cardiac Arrest (APACAR2) (NCT02527031), a randomized na study. The primary outcome is Number of Participants Surviving With Good Neurological Outcome (CPC 1 or 2) on Discharge From the ICU or at 6 Months.

2. Clinical Question

This is a comparison of two care strategies in a specific clinical context. It does not estimate the effect of ECMO compared with standard resuscitation without ECMO. Nor does the primary endpoint capture every aspect of survival, neurological status, or the process of delivering circulatory support. The outcome combines status at ICU discharge with status at 6 months, depending on the participant’s course as described in the record. The results therefore need to be read in light of that definition and the small number of randomized participants.

3. Trial Design

The registry describes APACAR2 as a randomized, parallel-group study with no masking. It compared pre-hospital ECMO insertion with in-hospital ECMO insertion for refractory cardiac arrest. The recorded enrollment was 65 participants, with 33 assigned to in-hospital ECMO and 32 to pre-hospital ECMO for the primary endpoint. The registry lists the study as completed.

Random allocation is intended to create groups that are comparable, on average, at the start of a trial. In an unmasked study, participants and study teams are not blinded to the assigned strategy. That is unsurprising for a comparison based on where a procedure is performed, but awareness of allocation can still matter for care processes and for outcomes that involve judgment. The registry record does not report further details about concealment of allocation or blinded outcome assessment.

The primary outcome was assessed in the intention-to-treat population, which the record defines as all randomized patients. The endpoint was a count of participants alive with CPC 1 or 2 at ICU discharge or at 6 months. Its stated timeframe allows follow-up through hospital stay, with an expected average of 6 weeks, or to 6 months. The endpoint description says the criterion is fulfilled at ICU discharge or, if applicable, when the participant is alive at 6 months with CPC 1 or 2.

The record lists additional outcomes concerning ECMO implementation, immediate complications, neurological status at later time points, and organ harvesting. Results are posted for only some of these outcomes. The registry record does not report the original sample-size justification, the detailed allocation procedure, or a complete statistical analysis plan. The randomized design supports a comparison of the assigned strategies, but it does not by itself resolve limitations arising from the small sample, incomplete reporting, or uncertainty around the estimates.

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

Analysis population for the primary outcome, as defined in the registry: The intention-to-treat (ITT) population included all randomized patients.

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 Number of Participants Surviving With Good Neurological Outcome (CPC 1 or 2) on Discharge From the ICU or at 6 Months, measured over At 6 months or participants will be followed for the duration of hospital stay, an expected average of 6 weeks.

The primary endpoint counts participants who survived with a good neurological outcome, defined as Cerebral Performance Category (CPC) 1 or 2. The registry specifies that the criterion is met if a participant is alive with CPC 1 or 2 at ICU discharge, or is alive with CPC 1 or 2 at 6 months. The stated timeframe is 6 months, with follow-up through the hospital stay for participants discharged from the ICU before then; the record describes hospital stay as an expected average of 6 weeks.

This endpoint combines survival and neurological status. It therefore distinguishes the outcome of interest from survival alone: being alive does not by itself meet the endpoint unless the specified CPC category is also present. Combining these dimensions can be useful when the clinical question concerns both whether participants survive and their neurological status, though it does not show each dimension separately. The registry’s posted primary result is a count of participants meeting the combined criterion in each randomized group.

The endpoint definition also means that assessment can occur at different points, according to the participant’s course. Readers should interpret the outcome using the registry’s stated rule, rather than treating it as a uniform assessment made at one identical visit for every participant. Further details about the handling of participants without an observed endpoint assessment are not reported in the registry record.

7. Results Posted in the Registry

• Pre Hospital ECMO: 21.9% (7/32) versus 27.3% (9/33) on control; risk difference -5.4 percentage points (95% CI -26.3 to 15.5), risk ratio 0.80 (0.34–1.89); unadjusted two-proportion z-test p = 0.614.

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.

Number of Participants With Success of the Implementation of ECMO

• 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:
  • Pre Hospital ECMO: 87.1% (27/31) versus 70.8% (17/24) on control; risk difference 16.3 percentage points (95% CI -5.4 to 37.9), risk ratio 1.23 (0.92–1.64); unadjusted two-proportion z-test p = 0.135.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre Hospital ECMO and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Immediate Complications: Haemorrhage

• 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:
  • Pre Hospital ECMO: 27.3% (6/22) versus 8.0% (2/25) on control; risk difference 19.3 percentage points (95% CI -2.2 to 40.7), risk ratio 3.41 (0.77–15.19); unadjusted two-proportion z-test p = 0.079.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre Hospital ECMO and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Immediate Complications: Infection

• 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:
  • Pre Hospital ECMO: 36.0% (9/25) versus 34.6% (9/26) on control; risk difference 1.4 percentage points (95% CI -24.9 to 27.6), risk ratio 1.04 (0.49–2.19); unadjusted two-proportion z-test p = 0.918.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre Hospital ECMO and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information about whether ECMO implementation was successful and about immediate complications. Across the posted secondary comparisons, the estimated differences are uncertain, and their confidence intervals include zero. This broad pattern does not provide a clear secondary signal that resolves the uncertainty in the primary comparison. It also does not establish that the groups are alike on these other outcomes.

These endpoints relate to the primary result by describing other aspects of the strategies: the feasibility of implementation and complications during the stated assessment periods. They address different questions from survival with good neurological outcome and should not be combined into a single conclusion. Some secondary results use fewer participants than were included in the primary endpoint analysis, so their estimates have additional limitations related to the available denominators.

The registry lists eight secondary outcomes, but results are posted for only some of them. Results for ECMO implementation time, neurological status at the later listed time points, and organ harvesting are not reported in the registry record. The record also does not list sponsor analyses for the secondary outcomes with posted counts. The comparisons shown are simple unadjusted recalculations rather than a set of reported confirmatory sponsor tests.

When many secondary outcomes are assessed, some differences may appear noteworthy by chance, even if there is no underlying effect. A prespecified hierarchy or adjustment for multiple testing can help control how such results are interpreted. Neither is reported in the registry record. For that reason, the secondary findings carry less weight than the primary analysis and are best viewed as descriptive context for the trial rather than independent evidence for a definitive conclusion.

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

• Number of Participants With Success of the Implementation of ECMO
• ECMO Implementation Time
• Number of Participants With Immediate Complications: Haemorrhage
• Number of Participants With Immediate Complications: Infection
• The Quality of Survivors' Neurological Status According to the CPC Neurological Classification at Day 28
• The Quality of Survivors' Neurological Status According to the CPC Neurological Classification at 2 Months
• The Quality of Survivors' Neurological Status According to the CPC Neurological Classification at 1 Year
• Number of Organ Harvesting

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either meets the definition of survival with CPC 1 or 2 or does not. The posted arm results are counts of participants meeting that definition, alongside the number in each group. For this kind of outcome, a comparison may be expressed as a difference in the proportion of participants with the event. The posted recalculation uses a risk difference, defined as the event proportion in the pre-hospital group minus the event proportion in the in-hospital group.

In general, a risk difference of zero corresponds to equal observed event proportions. Negative values mean the event proportion is lower in the first group named in the comparison; positive values mean it is higher. Here, the calculated risk difference is -0.054. Its interpretation depends on the specified event and the group order: the event is survival with CPC 1 or 2, and pre-hospital ECMO is compared with in-hospital ECMO. This numerical estimate is a sample-based comparison, not a direct statement about what would happen to every participant in either strategy.

The registry’s sponsor analysis uses a two-sided chi-square test. In general, a chi-square test evaluates whether the observed distribution of a categorical outcome across groups is compatible with the null hypothesis of no association between group and outcome. A two-sided test considers departures in either direction, rather than only a difference favoring one particular group. The registry reports p = 0.61. The recalculation gives p = 0.614, a simple unadjusted result from the posted summary statistics. The two values agree when rounded as in the registry report.

A p-value describes how unusual results at least as discrepant as those observed would be under the statistical model and a null hypothesis of no group difference. It is not the probability that the null hypothesis is true, nor does it measure the probability that the result will replicate. A larger p-value does not establish equality. It indicates that these data do not provide strong evidence against the no-difference null under the reported test. The estimated difference and its confidence interval are needed to see the range of effect sizes that remain compatible with the data.

A confidence interval expresses uncertainty around an estimated effect under the method used to construct it. For the primary risk difference, the interval extends from -0.263 to 0.155. Because it includes zero, the data are compatible with no difference as well as with effects in either direction. The interval is broad, so the estimate is not precise enough to narrow the plausible range to a small set of values. The interval is not a guarantee that the true value lies within it, and its coverage depends on the statistical assumptions and calculation method.

Randomization supports the interpretation of group comparisons by reducing systematic differences in treatment assignment. However, randomization does not ensure that every important characteristic is balanced in a small trial, and it does not remove uncertainty caused by the number of participants. The record identifies the primary analysis population as intention-to-treat, including all randomized patients. It does not report a detailed account of how missing outcome data were handled, or whether any alternative analysis populations were used.

The trial has one posted primary comparison and multiple secondary outcomes. When many outcomes are examined, the chance of seeing an apparently notable result by chance can increase. In general, multiplicity methods control or otherwise address this issue, while an outcome hierarchy can distinguish confirmatory tests from exploratory ones. The registry record does not report a multiplicity procedure, an outcome-testing hierarchy, or a complete statistical plan. Accordingly, secondary findings should not be treated as if they had the same confirmatory status as the primary endpoint.

The secondary recalculations are unadjusted comparisons based on posted summary statistics. They should be understood as descriptive supporting analyses rather than substitutes for the sponsor’s primary test. The registry does not list sponsor analyses for the secondary outcomes shown. The record also does not report whether interim analyses were planned or conducted, or the original rationale for selecting the enrollment target. Those aspects cannot be reconstructed from the posted results.

For binary outcomes, event counts and group denominators are central to interpretation. A difference in counts alone is not a valid comparison when group sizes differ; the relevant comparison accounts for each group’s denominator. The displayed risk differences and confidence intervals do this. More generally, sparse event data can make estimates unstable and intervals wide. This is especially relevant when secondary endpoints have fewer participants with available outcome data than the randomized primary population.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -0.054, with a 95% confidence interval from -0.263 to 0.155. The interval includes zero, so the posted data are compatible with no difference as well as with a lower or higher event proportion in the pre-hospital group. The width of the interval indicates substantial uncertainty about the magnitude and direction of the difference.

A confidence interval is not a range containing all plausible clinical interpretations, nor does it give the probability that the true effect lies inside its endpoints. In general, it describes uncertainty produced by a statistical procedure under its assumptions. It is useful because it shows that the point estimate alone does not summarize the evidence: values on both sides of zero remain compatible with the observed data.

The registry’s p-value and the recalculated p-value are both consistent with a result that does not clearly distinguish the strategies statistically. Neither should be interpreted as evidence of equivalence. Demonstrating equivalence or non-inferiority ordinarily requires a prespecified margin and an analysis designed around that question; such details are not reported in the registry record.

Precision is constrained by the number of participants and the number meeting the primary endpoint. The study enrolled 65 participants, and the endpoint counts are 9 and 7. A larger dataset could, in general, produce a narrower interval, but the registry’s planning illustrations are not evidence that this trial had a particular target effect or level of power. The original design assumptions are not reported in the registry record.

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 section gives planning illustrations based on the observed effect, not the trial’s original design. For this binary endpoint, the values are participants per arm, not a total across both arms and not total events. Read each row as an illustration of the number of participants per group that would be needed under the stated planning assumptions to detect the stated fraction of the observed effect.

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 the stated fraction of the observed effect. The table presents separate columns for 80% and 90% power. In plain language, the 80% column describes a planning target that would give the test an 80% chance of detecting the specified effect if that effect were true and the assumptions held. The 90% column uses a higher chance of detection, which generally requires more participants.

The rows show how the illustration changes when planning for 100%, 75%, or 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants. The displayed figures are therefore highly dependent on the effect size selected for planning; they should not be read as a recommendation or as a reconstruction of the trial’s design.

These figures are not observed power. They are planning calculations based on the observed effect and stated assumptions, rather than a measure of the trial’s achieved ability to find a true effect. The registry record does not report the original sample-size justification or the assumptions used when the trial was designed. The table and curve are best used to understand how sample-size requirements vary across the displayed effect assumptions, not to infer what the investigators planned or what the results prove.

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 = 0.273; treatment proportion p₁ = 0.219; average p̄ = 0.246.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6089 = 1.1933.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6077 = 0.5114.
4. n = (1.1933 + 0.5114)² / (-0.0540)² = 997.5, rounded up to 998 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 <- 0.272727272727273                          # control proportion
p1 <- 0.21875                          # 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(2527031)
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 = 998 (80% power), 1,335 (90% power)
 75% of observed effect: n per arm = 1,807 (80% power), 2,419 (90% power)
 50% of observed effect: n per arm = 4,138 (80% power), 5,539 (90% power)
power.prop.test: 997.5 
Simulated power at n = 998 per arm: 0.799 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s posted primary analysis is a two-sided chi-square test comparing the randomized groups. It reports p = 0.61. The simple unadjusted recalculation from the posted summary counts gives p = 0.614, with a risk difference of -0.054 and a 95% confidence interval from -0.263 to 0.155. The recalculated p-value is consistent with the sponsor’s rounded result.

The recalculation offers a transparent way to view the group comparison using the posted counts. It is not a replacement for the sponsor’s analysis or for details that may be present in a fuller analysis plan. The record indicates no discrepancy between the sponsor result and recalculation. The sponsor’s own analysis is therefore the primary reported inferential result, while the recalculated estimate and interval help describe the size and uncertainty of the comparison.

The sponsor’s p-value does not show that the strategies are equal, and the recalculation does not change that interpretation. The confidence interval includes zero and extends in both directions, leaving substantial uncertainty. The registry does not report a sponsor statistical analysis for the secondary outcomes shown in the results summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and several secondary outcomes. It does not report how the investigators planned to control the risk of false-positive findings when examining multiple outcomes. No multiplicity adjustment or formal hierarchy for testing the outcomes is reported in the registry record. This matters because, in general, testing many outcomes increases the chance that at least one result may look unusual by chance.

The absence of a reported multiplicity procedure does not invalidate the posted counts. It does mean that secondary comparisons should be interpreted cautiously, particularly when they are considered alongside several other outcomes. The primary analysis has a clearly identified endpoint and a reported sponsor test; the secondary results do not have the same level of reported inferential detail.

The primary population is described as intention-to-treat and includes all randomized patients. That definition is useful because it ties the primary comparison to randomized assignment. However, the record does not explain how missing endpoint assessments were handled, whether every randomized participant had complete outcome information, or whether any imputation or sensitivity analyses were used. The detailed flow of participants through follow-up is not reported.

The registry record also does not report a complete statistical analysis plan, the original sample-size justification, interim analyses, or a detailed account of allocation concealment and outcome assessment. These omissions limit assessment of whether all analyses were prespecified and how decisions were made before the results were known. They do not justify assuming that particular procedures were or were not used; those details are simply not reported in the registry record.

Given these reporting limits, interpretation should emphasize the defined primary endpoint, the posted randomized group counts, the sponsor’s reported test, and the uncertainty expressed by the interval. Claims based on individual secondary outcomes or on unreported analytic choices would go beyond what the registry record establishes.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: haemorrhage (60.0%), disseminated intravascular coagulation (39.3%), shock (39.3%), cardiac failure acute (35.7%), peripheral ischaemia (30.0%).

The registry reports serious adverse event information separately by group. For in-hospital ECMO, 28 participants were listed as at risk for serious adverse events and 26 as affected; for pre-hospital ECMO, the corresponding figures were 30 and 24. The listed deaths were 24 and 26, respectively. These figures describe the safety reporting fields in the record and should be read with their denominators in view.

The registry also lists the most frequent serious adverse event terms with percentages, including haemorrhage at 60.0%, disseminated intravascular coagulation at 39.3%, shock at 39.3%, acute cardiac failure at 35.7%, peripheral ischaemia at 30.0%, and pneumonia at 25.0%. The percentages are registry entries; the record excerpt does not provide enough information to infer whether terms represent unique participants, event episodes, or overlapping categories. They should not be added together or interpreted as mutually exclusive groups.

For other adverse events, the record lists 33 participants at risk and 0 affected in the in-hospital group, and 32 at risk and 0 affected in the pre-hospital group. Safety data have their own reporting denominators and should not be assumed to match every efficacy analysis population. These data are descriptive; the registry does not report a comparative safety analysis for these figures.

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

The posted primary results describe a randomized comparison of two ECMO implementation strategies among people with refractory cardiac arrest. The endpoint counts participants alive with CPC 1 or 2 at ICU discharge or at 6 months. The observed counts were 9 of 33 for in-hospital ECMO and 7 of 32 for pre-hospital ECMO. The sponsor’s two-sided chi-square test reports p = 0.61, and the recalculated risk difference has a confidence interval that includes zero.

These data do not show a statistically clear difference between the strategies on the primary endpoint. They also do not show that the strategies are equivalent, or establish that any difference is absent. The interval is broad and compatible with effects in either direction. The limited number of participants and endpoint events means that the result is imprecise.

The trial’s question is specifically about pre-hospital versus in-hospital ECMO insertion. It does not estimate the effect of ECMO relative to resuscitation without ECMO. The primary endpoint combines survival and neurological status, and its assessment timing follows the registry’s discharge-or-6-month rule. Results cannot be generalized beyond that defined comparison and outcome without additional evidence.

The secondary outcomes may help describe implementation and complications, but their reporting is incomplete and no sponsor analyses are listed for the posted secondary results. The registry does not report multiplicity handling, missing-data methods, or a complete statistical plan. Those gaps make it especially important not to treat isolated secondary findings as conclusive.

Overall, the registry provides a small randomized comparison with a reported primary test and a broad interval around the estimated difference. It allows readers to see the observed results and their uncertainty, but it does not support a definitive claim that one strategy is better, worse, or equivalent on the primary outcome.

18. Why This Trial Matters Statistically

This trial raises statistical issues that are common in studies of urgent, complex care strategies. The comparison is randomized, but the total enrollment is small, and the primary endpoint is met by a limited number of participants. In that setting, a point estimate can be unstable and the confidence interval can remain broad. The distinction between a non-significant test and evidence of equivalence is particularly important.

The outcome also combines survival with neurological status and permits assessment at ICU discharge or at 6 months. This definition has clinical relevance to the question posed, but its timing is not identical for every participant. Clear endpoint definitions and transparent reporting of assessment and missing-data handling are therefore important for interpreting results across groups.

The trial illustrates the value of reporting an effect estimate and confidence interval alongside a p-value. The sponsor’s test summarizes evidence against a no-difference hypothesis, while the risk difference and interval show the direction, scale, and uncertainty of the estimated comparison. Together, these are more informative than a p-value alone.

Finally, the secondary results and planning illustrations show why a registry record should be read with attention to analysis status and assumptions. Secondary outcomes are not automatically confirmatory, and sample-size illustrations based on an observed effect are not the original design plan or observed power. Distinguishing these elements helps keep conclusions aligned with what the trial actually reports.

19. Limitations

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

The main limitation for interpretation is the small randomized sample: enrollment was 65, divided between groups of 33 and 32 for the primary endpoint. The primary event counts were also limited. Consequently, the estimate is imprecise, and the confidence interval allows effects in either direction. A result without a clear statistical difference should not be read as proof of no meaningful difference.

The endpoint combines survival and neurological status and uses an assessment at ICU discharge or at 6 months. The registry describes the rule, but further detail about outcome assessment, adjudication, and the handling of missing outcomes is not reported in the registry record. The record does not show whether all randomized participants had complete primary outcome data or how any unavailable assessments were handled.

Although the study is randomized, it is not masked. The record does not report whether outcome assessors were blinded, or provide details about allocation concealment. Because the strategies differ in where ECMO is initiated, masking of care teams may not be feasible; the relevant assessment procedures are nevertheless not reported in the registry record.

Reporting is incomplete for secondary outcomes. The registry lists eight secondary outcomes but posts results for only some, and it does not list sponsor analyses for the secondary results shown. The record does not report multiplicity handling, a full statistical analysis plan, interim analyses, or the original sample-size justification. These omissions restrict evaluation of prespecification and the intended strength of secondary inferences.

Finally, the findings address the comparison of pre-hospital and in-hospital ECMO in the trial population. They do not directly answer questions about ECMO versus standard resuscitation, and the posted results do not establish broad applicability beyond the specific setting and outcome definition recorded.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Comparative Study Between a Pre-hospital and an In-hospital Circulatory Support Strategy (ECMO) in Refractory Cardiac Arrest (APACAR2) — NCT02527031.
• Registry record last updated 2026-06-30; status last verified 2026-03.
• Results first posted 2026-06-12.
• 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

APACAR2 was a completed randomized, parallel-group study with no masking, comparing pre-hospital with in-hospital ECMO insertion for refractory cardiac arrest. The registry records enrollment of 65 participants. The primary outcome was survival with CPC 1 or 2 at ICU discharge or at 6 months, assessed in the intention-to-treat population.

The primary counts were 9 of 33 in the in-hospital group and 7 of 32 in the pre-hospital group. The registry reports a two-sided chi-square p-value of 0.61. The recalculated risk difference is -0.054, with a 95% confidence interval from -0.263 to 0.155. This comparison is uncertain and does not establish a difference or equivalence.

Some secondary and safety results are posted, but secondary sponsor analyses, multiplicity methods, missing-data handling, the original sample-size justification, and a complete statistical plan are not reported in the registry record.