Intensive Alveolar Recruitment Protocol After Cardiac Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Intensive Alveolar Recruitment Protocol After Cardiac Surgery (NCT01502332), a randomized na study. The primary outcome is Severity of Pulmonary Complications in the Post-operative Period.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with triple masking. It is marked completed, with enrollment of 320. The sponsor is the University of Sao Paulo. The study start is recorded as 2011-12 and primary completion as 2014-02. The phase is listed as NA.

The comparison was between two protective mechanical ventilation strategies after cardiac surgery. Both used low tidal volume ventilation; the principal difference described in the registry was the intensity of alveolar recruitment and the PEEP used afterward. The intensive strategy used an opening pressure of 45 cmH2O and PEEP = 13 cmH2O. The moderate strategy used an opening pressure of 20 cmH2O and PEEP = 8 cmH2O.

The registry summary identifies patients with deficient gas exchange in the immediate postoperative period, using PaO2/FIO2 < 250 at a PEEP of 5 cmH2O. The summary says patients had a stabilizing period of four hours of controlled mechanical ventilation before routine weaning and physiotherapy. Further details of the allocation sequence, concealment, masking procedures and analysis populations are not reported in the registry record.

The primary outcome was pulmonary-complication severity during the postoperative hospital stay. Secondary outcomes listed include length of ICU stay, length of hospital stay, barotrauma and hospital mortality. Numeric results are posted for barotrauma and hospital mortality; results for the two length-of-stay outcomes 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.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Severity of Pulmonary Complications in the Post-operative Period, measured over Participants were followed for the duration of hospital stay..

The primary endpoint concerns severity of pulmonary complications during the postoperative period. The registry describes a score based on the highest complication grade reached during hospital stay. Its descriptions range from no complication and simple atelectasis through hypoxemia with abnormal lung findings, pneumonia or intense noninvasive ventilation need, and prolonged mechanical ventilation. The highest grade is death before hospital discharge. The registry describes grade 4 as a need for mechanical ventilation for more than 48 hours after surgery or after reintubation, and grade 3 as pneumonia or intense noninvasive ventilation need.

The posted arm values focus on the percentage of participants whose complication grade was 3 or higher. This grouping identifies more severe complications in the scale, while preserving less severe grades outside that threshold. The endpoint description says that the comparison itself used the ordinal variable, representing the highest score reached; the reported analysis used the Mann-Whitney U test. That distinction matters: an ordinal comparison uses the ordering of scores, whereas the displayed percentage reduces the score to whether a participant crossed a specified grade threshold.

In general, an ordinal measure can retain information about ordering without assuming that the steps between adjacent grades are equal. A threshold percentage is easier to interpret as an event proportion, but it does not show how scores are distributed within either side of the threshold. The registry does not report the full distribution of scores by arm.

7. Results Posted in the Registry

• Moderate Alveolar Recruitment: 25.8% (42/163) versus 15.3% (24/157) on control; risk difference 10.5 percentage points (95% CI 1.7 to 19.2), risk ratio 1.69 (1.07–2.65); unadjusted two-proportion z-test p = 0.021.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Incidence of Barotrauma

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Moderate Alveolar Recruitment: 1.2% (2/163) versus 0.0% (0/157) on control; risk difference 1.2 percentage points (95% CI -0.5 to 2.9); unadjusted two-proportion z-test p = 0.164.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Moderate Alveolar Recruitment and the control. The interval gives the range of effects that remain compatible with the data.

Hospital Mortality

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Moderate Alveolar Recruitment: 4.9% (8/163) versus 3.2% (5/157) on control; risk difference 1.7 percentage points (95% CI -2.6 to 6.0), risk ratio 1.54 (0.52–4.61); unadjusted two-proportion z-test p = 0.435.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Moderate Alveolar Recruitment and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes with posted numerical results cover barotrauma and hospital mortality. Their estimates are less conclusive than the primary binary comparison: the intervals for both outcomes include no difference and allow uncertainty about the direction and size of any contrast. The estimates should therefore be treated as imprecise rather than as confirmation of a consistent effect across outcomes.

The secondary pattern does not overturn or independently establish the primary finding. The primary endpoint is a severity score, with the sponsor comparing its ordinal distribution; the secondary outcomes represent distinct events. A difference in the primary endpoint can coexist with uncertain estimates for less frequent secondary events, and the secondary results cannot identify the mechanism behind the primary contrast.

The registry lists length of ICU stay and length of hospital stay as secondary outcomes, but numerical results for these outcomes are not reported in the registry record. Their absence means the full secondary-outcome pattern cannot be assessed from the posted results. No conclusions about those lengths should be drawn from the reported event outcomes.

Secondary analyses generally carry less evidential weight when many outcomes or comparisons are examined without a reported plan for controlling multiplicity. Each additional test creates another opportunity for a chance finding. The registry does not report a multiplicity adjustment or a prespecified hierarchy for secondary outcomes. The posted secondary p-values are therefore best treated as exploratory and interpreted with the estimates and their uncertainty, rather than as stand-alone confirmation.

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

• Length of ICU Stay
• Length of Hospital Stay
• Incidence of Barotrauma
• Hospital Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis reported by the registry is a Wilcoxon (Mann-Whitney) test comparing the postoperative pulmonary-complication score between the randomized groups. The score is ordinal: its categories have a rank order, but the registry does not say that the distance between neighboring grades is equal. In general, a rank-based comparison uses the ordering of observations rather than requiring normally distributed measurements or equal spacing between score categories. It can assess whether scores tend to be higher in one group, but the registry does not report a direct effect estimate for that comparison.

The posted percentages summarize a different form of the primary outcome: the proportion with pulmonary complications at grade 3 or higher. An unadjusted risk difference compares the two event proportions by subtracting the intensive-arm proportion from the moderate-arm proportion. The reported recalculated risk difference is 0.105. A positive value indicates a larger proportion in the moderate arm for this binary threshold. The confidence interval gives a range of values compatible with the recalculation under its statistical assumptions; it is not the result of the sponsor's ordinal test.

Other measures can express relative contrasts. The recalculated risk ratio is 1.686, with a confidence interval from 1.074 to 2.646; the recalculated odds ratio is 1.924, with a confidence interval from 1.1 to 3.363. In general, a risk ratio compares event probabilities, while an odds ratio compares event odds. These are unadjusted recalculations from the posted binary summaries and do not describe the full ordinal-score comparison. Their interpretation depends on the outcome definition and the selected threshold.

The unadjusted p-value for the primary binary recalculation is 0.021. A p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. The sponsor's p-value of 0.016 comes from the ordinal Wilcoxon analysis. Because the analyses address different outcome summaries, their p-values need not match.

For the secondary outcomes, the registry reports a logistic-regression analysis for hospital mortality with p = 0.267. The recalculated mortality comparison is unadjusted and reports p = 0.435. In general, regression can model an outcome in relation to a group indicator and other covariates, if included. The registry record does not report which covariates, if any, were included, so the precise model specification cannot be inferred. A regression result and an unadjusted comparison can differ because they may use different models or estimands; the record does not provide enough detail to attribute the difference to a particular cause.

For barotrauma, the posted binary comparison is an unadjusted recalculation. The interval includes zero, and its p-value is 0.164. In general, an interval that includes zero for a risk difference is compatible with no difference as well as with values on either side of zero. That does not prove equality; it indicates that the data do not estimate the contrast precisely enough to rule out no difference under the stated method.

Over-dispersion is relevant to analyses of counts or rates when variation exceeds what a simple model expects. The registry's primary outcome is described as an ordinal score, and its sponsor analysis is a rank-based test, not a count-rate model. Over-dispersion is therefore not a feature that can be assessed from the posted primary analysis. More generally, model choice should match the outcome scale and data structure rather than being selected solely by a p-value.

The registry does not report whether the primary analysis adjusted for baseline characteristics, how missing observations were handled, whether all randomized participants were analyzed as assigned, or whether there were interim analyses. The statistical analysis plan and the original sample-size justification are not reported in the registry record. Those omissions limit assessment of whether the reported analysis followed a prespecified plan and how robust it is to alternative assumptions.

11. Confidence Intervals and Precision

For the recalculated primary risk difference, the estimate is 0.105 and its confidence interval ranges from 0.017 to 0.192. The interval lies above zero, indicating that the posted binary comparison is compatible with a higher event proportion in the moderate arm than in the intensive arm. The width of the interval also matters: it allows a range of possible magnitudes, rather than identifying one exact effect. The registry does not report a confidence interval for its ordinal Mann-Whitney analysis.

In general, a confidence interval describes the uncertainty of an estimate under the method used. It is not a guarantee that the true effect lies within the particular interval, and it does not measure the probability that a treatment effect is clinically important. An interval excluding zero for a difference is consistent with a nonzero contrast under the calculation, but it does not remove concerns about outcome definition, missing data, or analysis choices.

Precision differs across outcomes. The barotrauma risk-difference interval ranges from -0.005 to 0.029 and includes zero. The mortality interval ranges from -0.026 to 0.060 and also includes zero. These intervals leave room for no difference and for effects in either direction. The mortality result is especially difficult to interpret from the point estimate alone because its interval is broad; the uncertainty should be considered alongside the estimate.

The arm percentages and the recalculated intervals address binary event summaries. They do not convey the full distribution of pulmonary-complication grades used by the sponsor's primary analysis. The registry's reported ordinal p-value has no accompanying effect estimate or confidence interval, so the magnitude and precision of the ordinal contrast cannot be read from that p-value alone.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They use two-sided significance level 0.05, equal allocation between the two arms and a normal approximation. The calculation uses the observed effect as its reference and considers detecting the stated fraction of that observed effect. The trial's original design assumptions and sample-size justification are not reported in the registry record.

For the primary binary recalculation, planning for 100% of the observed effect gives 232 participants per arm for 80% power and 311 participants per arm for 90% power. Planning for 75% of the observed effect gives 394 and 526 participants per arm, respectively. Planning for 50% of the observed effect gives 840 and 1,123 participants per arm, respectively. These are planning illustrations, not descriptions of enrollment in the trial.

The 80% power column represents a planning target for the chance of detecting the specified effect if the assumptions used in the calculation hold. The 90% power column uses a higher target and consequently requires more participants for the same effect assumption. Smaller effects are harder to distinguish from random variation, so the planning figures increase as the assumed fraction of the observed effect gets smaller. The figures are not observed power; they do not show the probability that the completed trial detected an effect after its results were known.

The hospital-mortality planning values are much larger because that calculation is based on the observed mortality contrast. They are also participants per arm, under the same stated planning assumptions. These calculations use the trial's observed effect as an input, which can be an unstable basis for planning when an estimate is imprecise. They should be read as illustrations of the consequences of the stated assumptions, not as recommendations or as evidence about the trial's original planning.

The sample-size curve should be interpreted alongside these assumptions: it conveys how planning requirements change as the target effect changes. The listed figures are per arm for these binary outcomes, not total event counts. For time-to-event outcomes, the stated convention would instead be total events, but these posted calculations are for the non-time-to-event comparisons.

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 = 0.153; treatment proportion p₁ = 0.258; average p̄ = 0.205.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5712 = 1.1195.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5664 = 0.4767.
4. n = (1.1195 + 0.4767)² / (0.1048)² = 232.0, rounded up to 232 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 <- 0.152866242038217                          # control proportion
p1 <- 0.257668711656442                          # 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(1502332)
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 = 232 (80% power), 311 (90% power)
 75% of observed effect: n per arm = 394 (80% power), 526 (90% power)
 50% of observed effect: n per arm = 840 (80% power), 1,123 (90% power)
power.prop.test: 232 
Simulated power at n = 232 per arm: 0.803 (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

For the primary outcome, the registry reports the sponsor's analysis as a Wilcoxon (Mann-Whitney) test of the ordinal pulmonary-complication score, with p = 0.016. This is the trial's own reported analysis. The recalculation uses the posted percentages for grade 3 or higher and produces an unadjusted risk difference of 0.105, with p = 0.021. The results are related because they concern the same underlying complication scale, but they summarize it differently: the sponsor's analysis retains the score ordering, while the recalculation classifies participants by a threshold.

The registry does not provide an effect estimate or confidence interval for the sponsor's ordinal analysis, so its magnitude cannot be directly compared with the risk difference. The p-values should not be read as competing estimates of the same quantity. The recalculated binary result is a supplementary view of the posted outcome, not a replacement for the sponsor's chosen ordinal analysis.

For hospital mortality, the sponsor reports logistic regression with p = 0.267, while the unadjusted recalculation has p = 0.435. The record does not give enough model detail to determine whether the regression included covariates or how it was specified. The difference between these values is not, by itself, evidence of an error; the procedures are not necessarily equivalent. For barotrauma, no sponsor analysis is reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry does not report whether the statistical plan adjusted for multiple testing across the primary and secondary outcomes, or whether any outcome hierarchy was prespecified. Multiplicity matters because interpreting many tests at once increases the chance that at least one result appears unusual by chance. Without a stated adjustment strategy, the reported secondary p-values should not be treated as if they were protected by a family-wise testing plan. The record also does not say whether additional analyses were conducted but not posted.

Missing-data handling is not reported in the registry record. It is not clear whether any primary outcome scores were unavailable, how missing scores were treated, or whether analyses used all randomized participants. The arm denominators are posted, but the registry does not explain the relationship between those denominators and the analysis population for each endpoint. No assumptions about imputation, censoring or complete-case analysis can be made from the available description.

The registry does not report an intention-to-treat designation, a per-protocol analysis population, exclusions after randomization, or sensitivity analyses. These details matter because departures from assigned treatment or loss of outcome information can affect the interpretation of a randomized comparison. The registry also does not report interim analyses or stopping rules, so none should be assumed.

The primary outcome is a ranked score, but the reported numeric arm values summarize a threshold rather than the full score distribution. No score-level summary or ordinal effect estimate is included with the reported test. That limits independent assessment of the sponsor's analysis and makes it difficult to evaluate whether the threshold summary captures the pattern across grades.

The original sample-size justification and the trial's planned statistical assumptions are not reported in the registry record. The posted planning illustrations are based on the observed effect and should not be confused with the original design rationale. These omissions do not invalidate the reported comparisons, but they restrict how fully their prespecification, completeness and robustness can be evaluated.

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 0% reporting threshold.

The adverse-event figures list zero serious adverse events and zero other adverse events for the intensive arm, and zero serious adverse events and zero other adverse events for the moderate arm. The corresponding at-risk counts are 157 for the intensive arm and 163 for the moderate arm. These figures describe what is recorded in the adverse-event summary; they do not establish that no events occurred outside the registry's reporting or ascertainment procedures.

The adverse-event record does not list deaths in those fields. Hospital mortality is reported separately as an outcome, so the zero adverse-event entries should not be interpreted as zero deaths. The registry does not report the adverse-event observation window, definitions, severity grading beyond the serious/other categories, or procedures for collecting events. Those omissions limit the safety interpretation.

In general, a zero count in a posted summary is not proof of zero risk. It can reflect the events captured and reported under the study's procedures, and the precision of a safety estimate depends on the amount and completeness of follow-up. The registry record does not provide enough detail to assess those aspects fully.

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

The primary result supports a distinction between two related summaries. The registry's own analysis compared the ordered pulmonary-complication score and reported p = 0.016. The posted threshold percentages and unadjusted recalculation indicate a higher proportion with complications at grade 3 or higher in the moderate arm than in the intensive arm, with a risk difference of 0.105 and a confidence interval from 0.017 to 0.192. These findings describe the recorded outcomes in this trial.

They do not establish that the intensive strategy should be used in clinical practice, or that it is effective or ineffective for every patient or setting. The trial concerns a specific postoperative population and compares strategies described by particular opening pressures and PEEP settings. The registry record does not provide enough information to assess how broadly the results apply beyond that population and those protocols.

The result also does not mean that every level of pulmonary complication differed in the same way. The recalculation collapses the score into grade 3 or higher versus lower grades, while the sponsor's test uses the ordinal score. The registry does not report the full score distribution or a sponsor effect estimate with a confidence interval, limiting understanding of the pattern and magnitude across grades.

Uncertain secondary findings should not be interpreted as proof that the strategies have identical effects on barotrauma or mortality. Their intervals include no difference, and the mortality estimate is imprecise. Results for length of ICU stay and length of hospital stay are not reported in the registry record. The safety summary also has limited detail about event ascertainment.

In general, statistical evidence is one part of interpreting a trial. The magnitude and precision of estimates, outcome definitions, analysis methods, missing data and relevance to the target population all matter. The registry results alone do not establish the clinical importance of the observed contrast.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint scale matters. The primary pulmonary-complication outcome is ordinal, but the posted percentages describe only whether participants reached grade 3 or higher. A rank-based comparison of the score and a binary comparison at a threshold answer related but distinct questions. Reporting both without conflating them helps readers distinguish a shift in the score distribution from a difference in the proportion crossing a chosen threshold.

It also shows why a p-value should not stand in for an effect estimate. The sponsor's ordinal test has a reported p-value but no effect estimate or confidence interval in the registry record. The unadjusted binary recalculation offers an absolute contrast and interval, but it does not recover the full ordinal result. Both the outcome scale and the uncertainty around an estimate are needed for a statistical reading.

The secondary outcomes illustrate the limits of sparse event evidence. Their intervals leave substantial uncertainty, and the registry gives no numeric results for two listed length-of-stay outcomes. A collection of secondary p-values cannot substitute for a prespecified analysis plan, especially when multiplicity handling is not reported.

Finally, the planning illustrations demonstrate how sample-size requirements depend on the assumed effect size. They are based on the observed effect and are not observed power or the trial's original design assumptions. Keeping planning exercises separate from the completed trial's results prevents a common interpretive error.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record has limited detail about the methods needed to assess the primary result fully. It identifies a randomized, triple-masked, parallel design, but does not describe sequence generation, allocation concealment, masking procedures or the analysis population. These details are not reported in the registry record, so the quality and implementation of those procedures cannot be assessed from the record alone.

The reported primary test compares the ordinal score, while the posted percentages focus on a grade threshold. The full score distribution and an effect estimate with confidence interval for the ordinal analysis are not reported. This limits assessment of how the result varies across the score categories and how precisely the sponsor's analysis estimates the group contrast.

The registry does not explain missing-data handling, deviations from assigned strategy, or whether analyses were adjusted for baseline characteristics. The logistic model for hospital mortality is not specified beyond its method label. The original sample-size justification, interim analyses, multiplicity strategy and statistical analysis plan are also not reported in the registry record.

Numeric results are not reported for length of ICU stay or length of hospital stay, though both are listed as secondary outcomes. The adverse-event summary lacks a stated observation window and detailed collection methods. These omissions limit interpretation of secondary and safety evidence. Finally, the primary result concerns a selected postoperative population with deficient gas exchange and the specific ventilation approaches described in the registry; generalization to other populations or protocols is not established by these data.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Intensive Alveolar Recruitment Protocol After Cardiac Surgery — NCT01502332.
• Registry record last updated 2016-11-23; status last verified 2016-10.
• Results first posted 2016-11-23.
• 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

NCT01502332, titled Intensive Alveolar Recruitment Protocol After Cardiac Surgery, is a completed randomized, triple-masked, parallel trial sponsored by the University of Sao Paulo. The registry records enrollment of 320 and compares intensive with moderate alveolar recruitment after cardiac surgery.

The primary outcome is postoperative pulmonary-complication severity. The sponsor reports an ordinal Wilcoxon (Mann-Whitney) analysis with p = 0.016. The posted threshold percentages and unadjusted recalculation show a risk difference of 0.105 for grade 3 or higher, with a confidence interval from 0.017 to 0.192. These analyses summarize the outcome differently.

Secondary numerical results are posted for barotrauma and hospital mortality; numeric length-of-stay results are not reported in the registry record. Important details concerning missing data, multiplicity and the original design assumptions are also not reported.