Multicenter Infection Surveillance Study Following Open Heart Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Multicenter Infection Surveillance Study Following Open Heart Surgery (NCT00673712), a randomized phase 4 study. The primary outcome is Hospital Acquired Pneumonia.

2. Clinical Question

The clinical question is about the observed frequency of a postoperative infection outcome in the two assigned groups. It is not a direct comparison of pain relief, opioid exposure, or every possible postoperative complication: those outcomes are not identified as the primary endpoint in the registry record. Nor does the posted comparison by itself establish why any difference occurred. The population, intervention and comparator are defined by the trial record, while details needed to assess how broadly the result applies—such as eligibility criteria, participant characteristics and procedure mix—are not reported in the registry record.

3. Trial Design

The registry record describes a completed, randomized, parallel-group phase 4 study with no masking. Its title identifies the study as multicenter and concerns infection surveillance following open heart surgery. The listed enrollment is 647. The record gives a start date of 2008-04 and a primary completion date of 2012-09. These dates describe the study record; they do not by themselves specify the duration of follow-up for each participant.

Participants were assigned to continuous sternal block or opioid-based analgesia. The former used a continuous local-anesthetic infusion through the ON-Q Painbuster Silver Soaker system. The latter included patient-controlled analgesia, intramuscular and oral narcotics, and other analgesics. Because masking is listed as none, the registry record describes an unmasked study. It does not report whether outcome assessors were blinded or how pneumonia diagnoses were adjudicated.

The primary outcome was hospital-acquired pneumonia, measured as the number of participants with pneumonia diagnosed during hospitalization within 30 days postoperatively. The primary outcome population is described as all randomized subjects. The registry record also lists surgical site infection and hospital length of stay as secondary outcomes. Surgical site infection was recorded as a participant count over 30 days postoperatively; length of stay was reported as a mean in days for the primary admission.

Although randomization is reported, the method used to generate the allocation sequence, allocation concealment, stratification, and the handling of departures from assigned treatment are not reported in the registry record. The original sample-size justification and planned statistical analysis are also not reported in the registry record. No analysis is listed as reported, so the posted group summaries and comparisons should be read as the results available in this record, not as a complete account of every analysis that may have been conducted.

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: all randomized subjects

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 Hospital Acquired Pneumonia, measured over 30 days postoperative.

The primary endpoint is the number of participants with hospital-acquired pneumonia diagnosed during hospitalization, assessed within 30 days postoperatively. The record defines the primary outcome population as all randomized subjects. The endpoint is binary at the participant level: each person is classified according to whether the specified event occurred, and the group results are presented as counts.

This endpoint is used to address the study’s stated interest in the relationship between pain management and pneumonia after cardiac surgery. A participant count makes the outcome interpretable as the frequency of an event in each randomized group, while the comparison estimates how those observed frequencies differ. The endpoint is limited to pneumonia diagnosed during hospitalization within the stated postoperative timeframe. It does not encompass infections diagnosed outside that definition or after that timeframe, and the record does not give diagnostic criteria beyond the description of pneumonia diagnosed during hospitalization.

In the posted results, the continuous sternal block group had 8 participants with the event among 321, and the opioid-based analgesia group had 18 among 326. The reported comparison is a risk difference, with opioid-based analgesia compared against continuous sternal block. That estimate describes the observed group contrast; it does not alone establish a causal mechanism or settle whether the difference is precise enough to support a firm conclusion. Interpretation also depends on how outcomes were collected, how missing observations were handled, and the analysis plan, details that are not reported in the registry record.

7. Results Posted in the Registry

• Opioid Based Analgesia: 5.5% (18/326) versus 2.5% (8/321) on control; risk difference 3.0 percentage points (95% CI 0.0 to 6.0), risk ratio 2.22 (0.98–5.02); unadjusted two-proportion z-test p = 0.050.

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.

Surgical Site 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:
  • Opioid Based Analgesia: 5.8% (19/326) versus 5.3% (17/321) on control; risk difference 0.5 percentage points (95% CI -3.0 to 4.1), risk ratio 1.10 (0.58–2.08); unadjusted two-proportion z-test p = 0.768.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Opioid Based Analgesia and the control. The interval gives the range of effects that remain compatible with the data.

Hospital Length of Stay

• 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:
  • Opioid Based Analgesia: mean 9.50 versus 8.80 on control; difference 0.70 (95% CI -3.89 to 5.29), standardized effect d = 0.02; z-test p = 0.765.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Opioid Based Analgesia and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover a different infection endpoint and a hospital-use measure. Together, they offer context about whether the pattern in the primary pneumonia comparison is echoed across other outcomes, but they do not establish one unified effect. The posted comparisons for these secondary outcomes are unadjusted, and the registry record does not report a plan for controlling the chance of misleading findings across multiple outcome tests.

Neither secondary comparison gives a precise, decisive contrast in the posted results: their confidence intervals include the relevant no-difference value, and their unadjusted p-values are 0.768 and 0.765. This pattern does not confirm the primary finding, but it also does not show that the groups are equivalent on those outcomes. A wide interval can remain compatible with a range of effects even when the point estimate is close to no difference. The secondary results should therefore be treated as contextual evidence rather than as definitive tests that settle the primary comparison.

Multiplicity matters because examining several outcomes creates more opportunities for an apparently notable result to arise by chance. Whether and how to adjust depends on the trial’s prespecified questions and analysis strategy. The registry record does not report whether these outcomes were hierarchically ordered, designated confirmatory or exploratory, or adjusted for multiplicity. Without that information, each unadjusted result warrants more caution than a single prespecified primary comparison, and the primary result should not be interpreted in isolation from the broader set of outcomes.

The registry’s stated aims included examining hospital-acquired pneumonia, surgical infection and patient outcomes including length of hospital stay. The posted secondary findings address only some of that broader context. They do not demonstrate that infection outcomes and length of stay are related to one another, because no such association analysis is reported. Nor do they explain mechanisms or establish whether differences in one outcome account for differences in another. The safest reading is that the secondary summaries are descriptive comparisons, with uncertainty and multiplicity limiting the weight that can be placed on them.

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

• Surgical Site Infection
• Hospital Length of Stay

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome, reported as the number of participants with hospital-acquired pneumonia. For a binary outcome, each participant contributes an event or a non-event according to the endpoint definition. The group event counts and group sizes are the basic information behind a comparison of event risks. The registry record presents a risk difference, which expresses the contrast between the event risks in the two groups on the risk scale. The direction of the reported comparison is opioid-based analgesia against continuous sternal block; a positive estimate therefore corresponds to a higher observed event risk in the former group under that ordering.

The posted risk difference is 0.030, with a confidence interval from < 0.001 to 0.060. The record also gives a risk ratio of 2.215 with a confidence interval from 0.977 to 5.022, and an odds ratio of 2.287 with a confidence interval from 0.980 to 5.337. These are different ways to express a contrast between binary outcomes. A risk difference is an absolute contrast, while a risk ratio compares risks proportionally and an odds ratio compares odds. They answer related but not identical descriptive questions, so their numerical values should not be treated as interchangeable. The posted registry comparison names risk difference as its metric.

The unadjusted p-value for the primary comparison is 0.05. A p-value is calculated under a statistical model and a null hypothesis; it describes how compatible the observed data are with that model, not the probability that a treatment effect exists. “Unadjusted” indicates that the reported p-value is not adjusted for other comparisons in the information posted. The registry record does not report the test used, any covariate adjustment, or a prespecified threshold for interpretation. It is therefore important not to infer a fuller statistical method than the record documents.

What does a confidence interval describe?

In general, a confidence interval gives a range of effect estimates compatible with the observed data under the interval’s statistical assumptions. It communicates uncertainty more directly than a point estimate alone. It is not a range that guarantees the true effect lies within it, and it does not resolve bias or problems in outcome measurement. The width of an interval reflects statistical precision, but precision is only one part of an evidence assessment. Design and analysis choices also matter.

For a difference measure, the no-difference value is zero. The primary interval begins at < 0.001, very close to that reference value. For a ratio measure, the no-difference value is one; the posted confidence intervals for the risk ratio and odds ratio extend across that value. Such measures can appear to give different impressions because they use different scales, and because their intervals are calculated for different estimands. The registry record does not report a formal method for reconciling these measures or identify one as a confirmatory analysis beyond listing risk difference for the comparison.

Why distinguish counts from continuous outcomes?

The secondary surgical site infection endpoint is also binary and is reported as participant counts. Hospital length of stay is continuous and is summarized by a mean and standard deviation in each group. For a continuous measure, a mean difference compares group averages, while the standard deviation describes spread among observations within each group. The posted length-of-stay mean difference is 0.7 days, and the comparison includes a confidence interval. The registry record reports standard deviations of 29.9 and 29.6 days, respectively. A mean and standard deviation do not show the full shape of the length-of-stay distribution; the record does not report distributional details or transformations.

Why can over-dispersion matter?

In general, a count model may assume a particular relationship between the average event count and its variability. Over-dispersion occurs when the observed variation is greater than the model allows; if it is ignored, uncertainty can be understated and tests can be misleading. The primary endpoint is posted as the number of participants with a binary event, not as a rate of repeated events, and no over-dispersion model is reported. Thus over-dispersion is a general statistical consideration rather than a method documented for this trial. The record does not state whether any alternative variance method was used.

What does randomization contribute?

In general, random assignment is intended to make treatment groups comparable on average with respect to both measured and unmeasured baseline factors. That rationale depends on how assignment is implemented and on the analysis preserving the randomized comparison. The registry identifies the study as randomized, but details of sequence generation, concealment, adherence, crossover, and analysis population are not reported in the registry record. The primary endpoint is described as applying to all randomized subjects, but the posted summaries alone do not show how missing outcome data, if any, were handled.

These methods concepts explain how to read the posted statistics; they do not fill gaps in the record. In particular, the trial’s planned statistical test, adjustment strategy, missing-data procedures and any interim analyses are not reported in the registry record. No analyses are listed as reported beyond the posted comparisons, so the estimates should be understood in the context of those documentation limits.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.030, with a confidence interval from < 0.001 to 0.060. The interval conveys that the point estimate should not be read as exact: a range of effects remains compatible with the posted data under the interval’s assumptions. Its lower bound is close to zero, the no-difference value for a risk difference. The estimate is therefore near that reference at the lower end while the interval also allows larger positive differences.

The registry also reports a risk ratio of 2.215, with a confidence interval from 0.977 to 5.022, and an odds ratio of 2.287, with a confidence interval from 0.980 to 5.337. Both ratio intervals include one, the no-difference value on those scales. The values and intervals depend on the measure used; they should be read as alternative descriptions of the binary-outcome contrast, not as independent confirmations.

For surgical site infection, the risk-difference interval extends from -0.03 to 0.041. For hospital length of stay, the mean-difference interval extends from -3.885 to 5.285. Each includes its measure’s no-difference value. Those intervals show that the estimates do not narrowly pin down a single contrast. They do not prove equivalence or rule out effects that may matter in context. The registry record does not report a threshold for clinical importance, so statistical precision cannot be translated into a judgment about clinical relevance.

Confidence intervals account for sampling uncertainty under their statistical assumptions. They do not account automatically for bias from outcome ascertainment, missing observations, departures from the analysis plan, or selective reporting. The registry record does not provide enough detail to assess those sources of uncertainty. Precision should therefore be considered alongside the randomized design, the unmasked status and the limits of the reported methods.

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 illustrative calculations based on the observed effect, not the trial’s original design justification. The record specifies a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The displayed figures are participants per arm for 80% power and participants per arm for 90% power; they are not total event counts.

The 80% power column describes a planning target: under the stated assumptions, a study designed at that size would have an 80% chance of detecting the selected effect using the assumed test procedure, if that effect were the true effect and the assumptions held. The 90% column uses a higher power target and therefore gives a larger planned number of participants per arm. These values are not a guarantee about any particular future study, because actual results depend on the true effect, event frequency, data quality and analysis.

Rows for 100% of the observed effect use the full effect estimate from the posted comparison. Rows for 75% and 50% of the observed effect illustrate smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants under the same planning assumptions. The resulting counts are planning illustrations only. They are not observed power, and they do not describe how much power the completed trial had under its original design assumptions. Those original assumptions and the trial’s own sample-size justification are not reported in the registry record.

For the primary pneumonia endpoint, the planning figures are 657 participants per arm for 80% power and 879 for 90% power when planning for 100% of the observed effect; 1,063 and 1,422 for 75%; and 2,151 and 2,878 for 50%. The corresponding values for the secondary endpoints are specific to their own observed estimates and are not directly interchangeable. Because the calculations are driven by observed effects, they should be read as illustrations of the relationship between effect size and required enrollment, not as a recommendation or a retrospective verdict on trial design.

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 = 0.025; treatment proportion p₁ = 0.055; average p̄ = 0.040.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2774 = 0.5436.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2765 = 0.2327.
4. n = (0.5436 + 0.2327)² / (0.0303)² = 656.8, rounded up to 657 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 <- 0.0249221183800623                          # control proportion
p1 <- 0.0552147239263804                          # 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(673712)
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 = 657 (80% power), 879 (90% power)
 75% of observed effect: n per arm = 1,063 (80% power), 1,422 (90% power)
 50% of observed effect: n per arm = 2,151 (80% power), 2,878 (90% power)
power.prop.test: 656.8 
Simulated power at n = 657 per arm: 0.811 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and two secondary outcomes, but it does not report a detailed statistical analysis plan. In particular, it does not state whether the secondary outcomes were confirmatory or exploratory, whether a hierarchy was prespecified, or whether any correction for multiple comparisons was planned. The posted p-values are unadjusted. When multiple outcomes are tested, interpreting each p-value as though it were the only test can overstate the strength of evidence. The missing multiplicity plan makes it difficult to determine how the collection of results was intended to support formal conclusions.

The record identifies the primary outcome population as all randomized subjects. It does not describe the analysis population used for each posted comparison, whether the groups were analyzed according to randomized assignment, or how protocol deviations and treatment changes were handled. Although the design is listed as randomized, the registry does not report the sequence-generation method or allocation concealment. These omissions limit assessment of how the randomized comparison was implemented and analyzed.

Missing outcome data are also not addressed in the posted description. The record does not report whether every randomized participant had outcome status available, how missing pneumonia or surgical site infection assessments were treated, or whether any sensitivity analyses were performed. For length of stay, it does not explain how incomplete admissions or unusual observations were handled. The listed arm sizes and outcome counts do not substitute for a missing-data account.

The registry record does not report interim analyses, stopping rules, prespecified subgroup analyses, covariate adjustment or procedures for selecting among analyses. It also does not provide a sample-size justification for the trial’s original design. These items should not be inferred from the posted results or from the planning illustrations. The absence of these details does not prove that no such procedures existed; it means they are not reported in the registry record. Consequently, the available results can be described, but their prespecification, robustness to missing data and place within a complete analysis strategy cannot be independently assessed from this record.

15. 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.

The serious adverse-event summaries list 0 serious events among 321 participants at risk in the continuous sternal block group and 0 among 326 at risk in the opioid-based analgesia group. The other adverse-event counts are also listed as 0 in both groups. These are the posted counts for the registry’s safety fields; they do not establish that no adverse events of any kind occurred or that the interventions have equal safety.

The record lists no serious adverse-event terms. Deaths are not reported as a numeric count in the posted safety information. A zero count in a registry summary should be distinguished from an unreported value: the latter cannot be interpreted as zero. The record does not provide a detailed account of event definitions, collection procedures, observation time for safety outcomes, severity categories, or causal attribution.

These safety figures should be read as limited descriptive reporting rather than a comprehensive safety comparison. The primary outcome and secondary outcomes concern infection and hospital stay, while the adverse-event summaries provide only the counts listed in the record. More detailed conclusions about safety are not supported by these fields alone.

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

The registry reports fewer participants with hospital-acquired pneumonia in the continuous sternal block group than in the opioid-based analgesia group, and it reports a positive risk-difference estimate when the latter group is compared with the former. The confidence interval and p-value describe the statistical uncertainty associated with that comparison under the methods used to produce them. They do not establish that one approach caused a difference, nor do they prove that a difference is absent.

The distinction between an estimate and a conclusion is important. A point estimate is one summary of the observed data; its confidence interval shows that the data do not identify a single exact value with high precision. The p-value is not a probability that the result is due to chance or that a treatment effect is true. In addition, the registry record does not report the full statistical plan, outcome-assessment procedures, missing-data handling or multiplicity strategy. Those limits make it inappropriate to turn the posted comparison into a broad causal or clinical claim.

The endpoint is specifically pneumonia diagnosed during hospitalization within 30 days postoperatively. It does not represent every infection, every postoperative complication, or outcomes beyond that definition. The record also includes surgical site infection and hospital length of stay, but their posted summaries do not establish that these outcomes are related to pneumonia or to each other. No conclusion about pain control, medication exposure, patient experience, or overall recovery follows from the primary endpoint alone.

The randomized design is relevant because random assignment is intended to support fair comparisons, but interpretation also depends on how randomization was carried out and how participants and outcomes were handled. The record identifies the trial as unmasked and does not report details about assessment or analysis. The results therefore support a careful description of the posted group summaries, not medical advice or a definitive determination that either analgesia approach works or does not work.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to interpret an uncommon binary outcome in a randomized clinical comparison. The pneumonia result is reported as participant counts as well as a risk difference and ratio measures. Looking across these summaries illustrates why effect estimates need both a clearly defined scale and an interval expressing uncertainty. A point estimate can appear specific while the data remain compatible with a range of contrasts.

The record also illustrates the importance of distinguishing a primary endpoint from secondary outcomes. Pneumonia, surgical site infection and hospital length of stay address related aspects of postoperative care, but they are not interchangeable measures. The secondary results cannot be treated as automatic confirmation or refutation of the primary comparison, especially when the registry does not report a multiplicity strategy. A statistical reading must retain the separate meaning and uncertainty of each outcome.

Another important issue is the gap between a completed randomized study and a fully documented analysis. The registry identifies key design features and posts group summaries, but does not report the original sample-size justification, detailed analysis methods, missing-data procedures or interim analyses. That distinction matters for reproducibility and for understanding whether the posted comparisons were planned and how they fit into the full evidence. Planning illustrations based on an observed effect can teach how sample-size requirements change as effects shrink, but they do not recover the trial’s original rationale.

Finally, the safety summary demonstrates why zeros and unavailable values must be distinguished. Posted zero counts describe the recorded fields, while an unreported death count remains unknown from the registry record. Careful reporting avoids turning limited registry fields into broader claims. Together, these issues make the study useful for learning how endpoint definition, effect scales, uncertainty, multiplicity and reporting completeness shape interpretation.

18. Limitations

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

Several limitations specific to this record constrain interpretation. The study is listed as unmasked, and the registry does not report whether pneumonia diagnoses or surgical site infections were assessed by blinded reviewers or adjudicated using prespecified criteria. Since the primary endpoint is described only as pneumonia diagnosed during hospitalization, the record does not provide additional diagnostic detail to judge consistency of ascertainment.

The record identifies the study as multicenter but does not report the number or characteristics of sites, the types of cardiac procedures represented, participant characteristics, or detailed eligibility criteria. It therefore does not allow a reader to assess how similar the enrolled population was to other cardiac surgery populations. The treatment descriptions also do not specify medication doses, treatment duration, adherence, or the exact implementation of analgesia beyond the information stated in the registry.

Although the trial is described as randomized, the sequence-generation and concealment methods are not reported. The record does not explain how missing outcome information, protocol deviations or treatment changes were handled, and it does not provide an analysis population for each comparison. These omissions limit assessment of potential bias and the robustness of the reported estimates.

The primary result is accompanied by uncertainty, and the secondary results also have intervals that include their no-difference values. The record does not state a clinical-importance threshold for any outcome. It also does not report a multiplicity strategy, detailed analysis plan or original sample-size justification. The adverse-event summary is limited: serious and other event counts are listed, but event definitions and collection details are not provided, and deaths are not reported as a numeric count. These limitations concern what can be evaluated from the registry record; they should not be taken as proof that unreported procedures or information did not exist.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Multicenter Infection Surveillance Study Following Open Heart Surgery — NCT00673712.
• Registry record last updated 2018-01-19; status last verified 2015-04.
• Results first posted 2015-05-04.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The record describes NCT00673712, a completed, randomized, parallel-group, unmasked phase 4 multicenter study of continuous sternal block versus opioid-based analgesia following cardiac surgical procedures. It lists enrollment of 647, a start date of 2008-04 and a primary completion date of 2012-09.

The primary endpoint was hospital-acquired pneumonia diagnosed during hospitalization within 30 days postoperatively. The posted counts were 8 of 321 for continuous sternal block and 18 of 326 for opioid-based analgesia; the reported risk difference was 0.030, with a confidence interval from < 0.001 to 0.060 and an unadjusted p-value of 0.05. Secondary outcomes were surgical site infection and hospital length of stay.

The registry record does not report a detailed statistical plan, missing-data methods, multiplicity procedures or the trial’s original sample-size justification. The posted estimates should be interpreted with those documentation limits in mind.