Rapid Sternal Closure System (TALON): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rapid Sternal Closure System (TALON) (NCT00638014), a randomized phase 4 study. The primary outcome is Percentage Change of Preoperative Incentive Spirometry (IS) Volume Achieved.

2. Clinical Question

The clinical question combines a short-term functional measure with a device comparison in cardiac surgery. Incentive spirometry volume is a measure of respiratory performance during recovery; it is not itself a direct measure of sternal wound infection or instability. Those complications were addressed as a secondary outcome. Accordingly, the primary and secondary questions capture different aspects of recovery and safety, and the result for one should not be treated as a result for the other. The registry does not report a separate primary question about long-term outcomes or a broader assessment of recovery.

3. Trial Design

The registry describes a randomized, controlled, phase 4 study using a parallel-group design. Participants were assigned to conventional wires only or to the Rapid Sternal Closure System supplemented with wires. The record identifies the study as single-masked, but does not state which participants or study personnel were masked, or how masking was maintained. The sponsor was Duke University. The study is listed as completed, with a start date of 2008-03 and primary completion in 2009-07.

Enrollment is recorded as 51. The arm-level summaries report 23 participants for conventional wires only and 28 for Talon. These are the group sizes associated with the posted primary results; the registry does not give a detailed accounting of participant flow, withdrawals, or exclusions from the analysis. The planned population is described broadly as cardiac surgical subjects at higher risk for sternal wound complications. Specific eligibility criteria and baseline characteristics are not reported in the registry record.

The primary objective was to evaluate early postoperative recovery through pain and pulmonary function. The posted primary endpoint concerns incentive spirometry volume, rather than pain. Secondary objectives concerned sternal wound complications, defined in the brief summary as surgically treated sternal wound infection and sternal instability or non-union. The listed secondary outcome combines infection and instability or non-union into one participant count, with follow-up up to 180 days.

The registry states that the null hypothesis for a given endpoint was no difference between groups and the alternative was a difference. More detailed original design assumptions, including the basis for the planned enrollment and the original statistical analysis plan, are not reported in the registry record. The record also does not specify the allocation ratio in its design description, although the posted arm sizes are available. The single-masking label alone does not establish who was masked.

4. Participant Flow and Accounting

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

Before assignment: Overall 53 subjects were consented and enrolled in the study from April 2008 to July 2009. Two patients were not included in the analysis (1 patients' surgery was cancelled, 1 patient was not randomized due to logistical reasons), leaving a total of 51 subjects who were included in the modified intent-to-treat analysis.

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 Percentage Change of Preoperative Incentive Spirometry (IS) Volume Achieved, measured over Baseline, Maximum value during postoperatively days 1 thru 7.

The primary endpoint is the percentage change of preoperative incentive spirometry volume achieved. The registry says maximum incentive spirometry volume was measured before surgery and then daily from postoperative day 1 through postoperative day 7, or discharge if earlier. The primary result summarizes change from the preoperative baseline using the maximum postoperative value during that interval. The instrument named in the record was a Coach 2 incentive spirometer with a one-way valve.

This endpoint was selected to represent an aspect of early postoperative respiratory recovery. Incentive spirometry asks a participant to achieve a measured inspiratory volume; change from baseline therefore provides a functional measure that can be compared between the randomized groups. It is not a direct measurement of pain, wound healing, infection, or sternal stability. Although the brief summary names decreased pain and improved pulmonary function as the primary objective’s intended manifestations of recovery, the posted primary endpoint specifically reports spirometry volume. A separate primary pain result is not reported in the registry record.

For continuous outcomes, a group mean describes the average observed value, while a standard deviation describes the spread of individual values around that mean. The reported arm means were 58.0 for conventional wires only and 67.0 for Talon, with standard deviations of 24.0 and 32.0, respectively. These summaries describe the posted endpoint; they do not by themselves establish how precisely the difference between group means is estimated. The comparison estimate and its confidence interval are needed to assess that uncertainty.

7. Results Posted in the Registry

• Talon: mean 67.00 versus 58.00 on control; difference 9.00 (95% CI -6.38 to 24.38), standardized effect d = 0.31; z-test p = 0.252.

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 Sternal Wound Infection or Sternal Instability/Non-union

• 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:
  • Talon: 3.6% (1/28) versus 4.3% (1/23) on control; risk difference -0.8 percentage points (95% CI -11.6 to 10.0), risk ratio 0.82 (0.05–12.42); unadjusted two-proportion z-test p = 0.887.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Talon and the control. The interval gives the range of effects that remain compatible with the data.

The study’s listed secondary outcome combines sternal wound infection with sternal instability or non-union. The posted count is one participant in each arm, with follow-up up to 180 days. The re-calculated comparison is close to no difference, but its uncertainty extends in both directions. With so few events, the result does not precisely distinguish the groups on this complication outcome.

The secondary endpoint concerns wound complications, whereas the primary endpoint measures change in incentive spirometry volume. The two outcomes address related aspects of postoperative care but are not interchangeable. The primary result cannot establish what happened to wound complications, and the sparse secondary result cannot determine the effect on pulmonary function. Together, the outcomes offer separate, limited views of the study’s objectives rather than a single overall measure of recovery.

Unadjusted secondary results generally carry less weight than a prespecified primary comparison because many secondary outcomes or analyses can increase the chance of findings that appear noteworthy by chance. In general, multiplicity adjustments or a clearly ordered testing plan can address some of that concern. The registry record does not report a multiplicity procedure, a testing hierarchy, or an inferential analysis for the secondary outcome. The result should therefore be treated as exploratory rather than as independent confirmation of the primary finding.

The registry lists one secondary outcome and does not report a sponsor analysis for it. It is not possible to tell from the record whether other secondary measures were planned but not posted, or whether the listed outcome represents the full secondary analysis plan. No conclusion about a broader set of wound outcomes should be drawn from this single combined measure.

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

• Number of Participants With Sternal Wound Infection or Sternal Instability/Non-union

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, so the posted summaries include a mean and standard deviation for each arm. The mean gives the average percentage change in incentive spirometry volume achieved. The standard deviation describes the observed spread of values within an arm; it is not the uncertainty around the arm mean and is not a confidence interval for the treatment-group difference. The reported means and standard deviations are 58.0 and 24.0 for conventional wires only, and 67.0 and 32.0 for Talon.

What does the mean difference represent?

The primary comparison uses a mean difference: the average in one arm contrasted with the average in the other. The re-calculated estimate is 9.0 on the reported percentage-change scale. This is a difference between group averages, not a claim that every participant experienced that change or that the difference applies uniformly across participants. The point estimate is only one part of the result; its uncertainty matters for interpretation.

The re-calculation is unadjusted and uses the posted group summaries. It does not account for participant-level covariates, nor can it reproduce an analysis based on individual measurements or other modeling choices not described in the registry. The sponsor reports a two-sided t-test, but does not give the underlying test statistic, estimated difference, or confidence interval. A t-test evaluates whether the data are compatible with a null hypothesis of no mean difference under its assumptions. A two-sided test considers departures in either direction.

How should the p-value be read?

In general, a p-value measures how unusual data at least as discrepant from a specified null model would be if that model were true, subject to the analysis assumptions. It is not the probability that the null hypothesis is true, and it is not a measure of the size or clinical importance of an effect. The re-calculated unadjusted p-value is 0.252, while the sponsor reports p = 0.41. Neither value, by itself, establishes equivalence or resolves the uncertainty in the estimated difference.

The registry’s reported analysis is identified as a two-sided t-test. The original analysis plan, including any adjustment, handling of repeated measurements, or details of the analysis population, is not reported in the registry record. The posted summary does not make it possible to determine whether the sponsor’s calculation used different data or analysis choices from the unadjusted re-calculation. There is no reported discrepancy flag, but the two p-values remain distinct reported results.

Why does the confidence interval matter?

In general, a confidence interval gives a range of estimates that are reasonably compatible with the data and the method used to construct it. A 95% confidence interval is not a statement that there is a 95% probability that the true effect lies in this particular interval. The re-calculated interval for the mean difference runs from -6.385 to 24.38. Because it includes no difference and extends in both directions, it indicates uncertainty about both the direction and size of the group difference. The registry does not report a confidence interval for the sponsor’s own analysis.

The standard deviations also show that individual observations vary within both arms. In general, larger variability makes a group mean difference harder to estimate precisely when other factors are held constant. A comparison based on summary statistics cannot show the shape of the individual measurements, identify unusual observations, or examine whether the results differ across participant subgroups.

What is the secondary comparison?

The secondary endpoint is binary: a participant either had the combined sternal wound infection or sternal instability/non-union outcome during follow-up, or did not. The registry reports one participant with the outcome in each arm, with follow-up up to 180 days. The re-calculation expresses the between-arm contrast as a risk difference. In general, a risk difference compares the event proportions between groups, whereas a risk ratio compares them multiplicatively. The posted secondary result is based on very few events, so its estimate and interval are especially sensitive to the observed event counts.

For binary outcomes, sparse events can produce wide uncertainty and unstable relative-effect estimates. In general, over-dispersion refers to observed variation greater than a model expects; it can make model-based uncertainty too small if ignored. The registry does not report an over-dispersion assessment or a model-based secondary analysis, and the low event count does not justify assuming a more elaborate model was used. The secondary endpoint has no sponsor-reported analysis listed in the record.

These methods describe statistical contrasts, not causal certainty beyond the study design and data. Randomization is intended to support a fair comparison, but the registry record does not report details of sequence generation, allocation concealment, adherence, or analysis population. The available summaries therefore support a limited interpretation of the posted comparisons, with particular caution about imprecision and unreported analytic choices.

11. Confidence Intervals and Precision

Precision concerns how tightly the available data estimate a group difference. The re-calculated primary mean difference is 9.0, and its 95% confidence interval extends from -6.385 to 24.38. That range includes no difference and values favoring either arm. The point estimate alone would conceal this uncertainty; the interval makes clear that the data are compatible with a range of possible differences. The registry does not report a confidence interval for the sponsor’s t-test result.

In general, a confidence interval is constructed by a method that would capture the underlying parameter in a stated proportion of repeated samples when its assumptions hold. It does not assign a probability to the parameter after observing these particular data. Its width reflects factors such as sample size, variability, and the analysis method. Here, the posted arm summaries have standard deviations of 24.0 and 32.0, while the arm sizes are 23 and 28. The interval’s breadth indicates that the estimate is not precise enough to pin down the magnitude or direction of the mean difference.

The secondary comparison is less precise still because the combined event was reported for one participant in each arm. Its re-calculated risk-difference interval crosses no difference and allows effects in either direction. Such sparse event data cannot establish that the complication risks are equivalent. The record does not report a precision target for that endpoint.

Confidence intervals should be read alongside endpoint relevance and the trial’s design, not as stand-alone evidence. The registry does not report a clinically important threshold for the primary endpoint or an acceptable margin for the secondary outcome. It is therefore not possible to determine from the interval alone whether every value it contains would be clinically unimportant or important.

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 expressed as participants per arm for the continuous primary endpoint and the binary secondary endpoint. They are not total event counts. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the model assumptions were correct. The 90% power column describes the analogous planning target at 90% power. These are design calculations, not guarantees about what a future study would observe. They are not observed power.

For the primary endpoint, planning for 100% of the observed effect gives 160 participants per arm for 80% power and 214 for 90% power. Planning for 75% of the observed effect gives 284 per arm for 80% power and 380 for 90% power; planning for 50% gives 638 and 854, respectively. Smaller effects require more participants because they are harder to distinguish from sampling variation.

The secondary endpoint’s planning figures are much larger: for 100% of its observed effect, 9,903 participants per arm are listed for 80% power and 13,256 for 90% power. The corresponding figures for 75% are 18,018 and 24,121, and for 50% are 41,470 and 55,516. The event-based estimate is highly uncertain because the observed event count is sparse; these illustrations should not be treated as a reliable forecast or as evidence that the original trial was designed to detect the observed difference.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 9.000; pooled standard deviation σ = 28.685.
2. n = 2 × (1.96 + 0.842)² × 28.685² / 9.000² = 159.5, rounded up to 160 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
delta <- 9                      # observed difference in means
sigma <- 28.6854866240254                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(638014)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 160 (80% power), 214 (90% power)
 75% of observed effect: n per arm = 284 (80% power), 380 (90% power)
 50% of observed effect: n per arm = 638 (80% power), 854 (90% power)
power.t.test: 160.4 
Simulated power at n = 160 per arm: 0.793 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a two-sided t-test with p = 0.41. It does not provide a sponsor-reported mean difference or confidence interval, so the size and precision of that analysis cannot be compared directly with the re-calculated estimate. The sponsor’s analysis and the re-calculation should be kept distinct.

The unadjusted re-calculation uses the posted means, standard deviations, and arm sizes. It estimates a mean difference of 9.0 and gives a 95% confidence interval from -6.385 to 24.38, with an unadjusted p-value of 0.252. The registry record does not explain why its p-value differs from the sponsor’s reported value. It does not provide enough analysis detail to determine whether a different analysis population, endpoint construction, or other method accounts for the difference.

The record does not flag a discrepancy between the calculations. Still, the re-calculation is not a substitute for the sponsor’s analysis: it is a simple unadjusted analysis of posted summary statistics and may not reproduce the original analysis procedure. The sponsor’s reported result remains the sponsor’s stated finding, while the re-calculation is a transparent check based on the arm-level summaries. Neither p-value should be read as a measure of effect size, and neither resolves the uncertainty about the underlying difference.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or statistical tests are examined. In general, the more opportunities there are to identify an apparently unusual result, the more likely at least one result may appear notable by chance. Prespecifying a primary endpoint and limiting confirmatory claims to a planned testing strategy can help readers interpret a set of results. The registry identifies the spirometry measure as primary and lists a combined wound-complication endpoint as secondary, but a formal multiplicity strategy is not reported in the registry record.

The record does not state whether an adjustment for multiple comparisons was used, whether there was a hierarchy for testing outcomes, or whether interim analyses were planned or conducted. It also does not report whether subgroup analyses were specified. These omissions do not prove that such procedures were absent; they mean the registry record does not provide them. The reported p-values should therefore be understood as the stated individual results rather than as values known to control error across a full family of tests.

Missing-data handling is also not reported. The primary measurement was planned at baseline and daily during postoperative days 1 through 7, or discharge if earlier, but the record does not give the completeness of those measurements, how early discharge affected endpoint calculation, or how missing observations were handled. It does not specify whether the primary summary used all randomized participants, participants with available measurements, or another analysis population. Participant flow, withdrawal reasons, and exclusions from analysis are not reported in the posted results.

For the secondary outcome, the follow-up period is stated as up to 180 days, but the registry does not explain how incomplete follow-up was handled or whether all participants had the same opportunity for event ascertainment. The record also does not report adjudication procedures for the combined outcome. These details matter because missing outcome information or differences in ascertainment can affect interpretation, particularly when event counts are sparse.

The registry’s brief summary states a null of no difference and an alternative of a difference for a given endpoint. More detailed statistical methods, including adjustment covariates, assumptions for repeated measurements, and any sensitivity analyses, are not reported in the registry record. Their absence limits the ability to assess analytic robustness; it should not be filled in by assuming a particular protocol or analysis plan.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: renal failure (4.3%), chest tube entrapment between sternal halves (not talon) (3.6%).

The registry reports serious adverse events among 1 participant in the conventional-wires arm and 1 participant in the Talon arm. The at-risk counts shown are 23 and 28, respectively. No other adverse events are reported for either arm in these summaries. The record does not report death counts.

These figures are counts, not a complete assessment of the comparative safety profile. The registry does not provide event-level descriptions for the serious adverse events by arm, the timing of events, their relationship to the closure approach, or a detailed definition of seriousness. It lists renal failure at 4.3% and chest tube entrapment between sternal halves (not Talon) at 3.6% among the top serious adverse-event terms, but does not give enough context to attribute those terms to a specific arm or to determine their relationship to treatment.

Comparing the serious-event counts descriptively does not establish equal safety. The study is small, and the record offers limited detail about ascertainment and attribution. Absence of other reported events in the posted summary should not be interpreted as proof that no other events occurred.

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

The primary estimate describes an average difference in percentage change of incentive spirometry volume achieved between the randomized arms. Its confidence interval includes no difference and extends in either direction, so the posted data do not precisely establish the direction or size of the underlying difference. The sponsor’s reported test and the unadjusted re-calculation both leave substantial uncertainty, although they yield different p-values.

The result does not establish that the approaches are equivalent. Demonstrating equivalence requires a prespecified margin and an analysis designed to determine whether effects fall within that margin; neither is reported in the registry record. Likewise, a non-significant test is not proof that there is no effect. It means the analysis did not provide strong evidence against its null under the specified test.

The secondary wound-complication count is one in each arm. That observation is descriptive, and the sparse event data leave the between-group comparison imprecise. It cannot establish the absence of a difference in infection, instability, or non-union. Nor should it be treated as evidence about outcomes that were not measured or separately reported.

The registry’s stated objective included decreased pain and improved pulmonary function, but the posted primary result concerns incentive spirometry volume. A separate pain result is not reported in the registry record. The endpoint also covers early postoperative measurement rather than a broad, long-term assessment of function. The wound-complication outcome has follow-up up to 180 days, but the record does not supply details on completeness of follow-up.

These results should be understood as observations from a randomized study with limited posted information and uncertain estimates. They do not support medical advice or a treatment recommendation. In general, treatment decisions require a broader assessment of evidence and patient circumstances than a single trial’s statistical results can provide.

18. Why This Trial Matters Statistically

This study illustrates the distinction between an observed difference and a precisely estimated difference. The primary arm means are not identical, and the unadjusted estimate is positive, but the confidence interval is broad and includes no difference. Reporting the estimate together with its interval gives a more informative account than relying on a p-value alone.

It also shows why a sponsor-reported analysis and a summary-statistics re-calculation should be labeled separately. The sponsor reports a two-sided t-test with p = 0.41, while the unadjusted re-calculation gives p = 0.252. The registry does not explain the difference. Keeping each result tied to its method avoids presenting the re-calculation as if it were the sponsor’s original analysis.

The secondary outcome demonstrates the statistical challenge of rare events. One participant in each arm had the combined wound outcome, leaving little information for a precise comparison. A numerical risk contrast can still be calculated, but its uncertainty is large; the numerical estimate should not be mistaken for a stable conclusion about relative risk.

Finally, the planning illustrations show how sample-size requirements depend on the effect one aims to detect. Smaller assumed effects require larger samples under the stated planning assumptions. These calculations are not the original trial’s design justification, which is not reported, and they are not evidence about the probability that the observed trial result is true. Together, the endpoint, uncertainty, sparse secondary events, and unreported analysis details make this a useful example of why statistical interpretation must consider design and precision as well as point estimates.

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 posted record leaves important details unavailable for evaluating the primary analysis. It gives no participant flow, missing-data strategy, analysis-population definition, baseline characteristics, or detailed eligibility criteria. The primary endpoint involved repeated daily measurement through postoperative day 7 or discharge if earlier, but the registry does not explain how those repeated measurements were combined beyond the stated maximum value, or how incomplete measurements were handled.

The sponsor’s primary analysis is reported only as a two-sided t-test and p-value. Its effect estimate and confidence interval are not reported, and the registry does not explain why the unadjusted re-calculation gives a different p-value. The record also does not provide the original sample-size justification, detailed randomization procedures, allocation concealment, masking procedures, or interim-analysis information. These items are not reported in the registry record and cannot be inferred from the study’s design labels.

The primary endpoint is a short-term functional measure. Although the study objective mentions pain and pulmonary function, a separate pain result is not posted. The secondary outcome combines infection with instability/non-union, and its reported event count is sparse. The record does not supply separate component counts, event adjudication details, or full follow-up accounting.

Safety reporting is similarly limited in the posted summary. Serious adverse-event counts are available, but event attribution by arm and deaths are not reported. The listed serious-event terms lack enough context to interpret their distribution between groups. These limitations narrow what can be concluded from the posted data; they do not establish that additional information was never collected.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Rapid Sternal Closure System (TALON) — NCT00638014.
• Registry record last updated 2011-05-02; status last verified 2011-04.
• Results first posted 2011-05-02.
• 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

The registry describes a completed, randomized, controlled, parallel-group phase 4 study of sternal closure in cardiac surgical subjects at higher risk for sternal wound complications. It compared conventional wires only with the Rapid Sternal Closure System supplemented with wires. Enrollment is listed as 51, and the primary endpoint was percentage change of preoperative incentive spirometry volume achieved.

The posted primary means were 58.0 for conventional wires only and 67.0 for Talon. The unadjusted re-calculation estimates a mean difference of 9.0 with a 95% confidence interval from -6.385 to 24.38 and p = 0.252. The sponsor reports a two-sided t-test with p = 0.41. The secondary combined wound outcome was reported for one participant in each arm, with follow-up up to 180 days.

Both comparisons remain uncertain, particularly the sparse secondary event comparison. The registry record does not report the original sample-size justification, detailed missing-data procedures, or a multiplicity plan.