A Study of Tenecteplase for Restoration of Function in Dysfunctional Central Venous Catheters: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Tenecteplase for Restoration of Function in Dysfunctional Central Venous Catheters (NCT00395876), a randomized phase 3 study. The primary outcome is Percentage of Patients Who Had Restoration of Central Venous Catheter (CVC) Function Following a Single Administration of Study Drug.

2. Clinical Question

The question is about a defined catheter-function outcome at a specified assessment time. It compares the two randomized sequences on the proportion of patients meeting that outcome after the initial study drug. It is not a comparison of all possible catheter outcomes, nor does this primary measure describe restoration after later administrations.

Restoration was defined using both withdrawal and infusion criteria. For patients weighing >= 10 kg, it required successful withdrawal of at least 3 mL of blood or fluid and infusion of 5 mL of normal saline. For patients weighing < 10 kg, the criteria were withdrawal of at least 1 mL of blood or fluid and infusion of 3 mL of normal saline. The registry record does not report further information about how the outcome was adjudicated or how the two sequence groups were masked during that assessment.

3. Trial Design

The registry describes a completed Phase III, randomized, double-blind, placebo-controlled, parallel-group study. It reports that the trial was conducted at 24 centers in the United States and Canada and enrolled 100 adult and pediatric patients with dysfunctional central venous catheters. Random assignment was in a 1:1 ratio to an initial dose of placebo or tenecteplase.

The posted arm names describe sequences: Placebo + Tenecteplase + Tenecteplase (PTT) and Tenecteplase + Tenecteplase + Placebo (TTP). The brief summary identifies the randomized initial dose as placebo or tenecteplase. The registry record does not give fuller arm descriptions, so the sequence names should not be taken as a detailed account of every administration or its timing beyond what is stated for the reported outcomes.

The primary endpoint was assessed 120 minutes after the first dose and used the modified intent-to-treat population. The posted primary outcome group sizes are 47 for PTT and 50 for TTP. These endpoint group sizes are not interchangeable with the enrollment figure, and the registry record does not explain the difference. The recorded study start is 2006-11, and primary completion is recorded as 2008-06.

Randomization and double blinding are design features intended to limit differences in participant characteristics and expectations between groups. A placebo comparator provides a control for the initial-dose comparison. The registry record does not report the randomization procedure, allocation concealment details, masking procedures, stratification factors, or the original sample-size justification.

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: Three patients were randomized but not treated, therefore the modified intent to treat (MITT) analysis population was 97.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Modified intent to treat (MITT) population

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 of Patients Who Had Restoration of Central Venous Catheter (CVC) Function Following a Single Administration of Study Drug, measured over 120 minutes after first dose.

The primary endpoint is the percentage of patients whose central venous catheter function was restored following a single administration of study drug, assessed 120 minutes after the first dose. Restoration required successful withdrawal of blood or fluid and infusion of normal saline, using different stated volume criteria according to patient weight. This operational definition turns the clinical concept of restored catheter function into an outcome that can be counted consistently.

The endpoint is used to compare the proportion meeting that definition in the two randomized groups. A percentage is appropriate for a yes-or-no outcome: each patient either meets the stated restoration criteria or does not. The reported percentages therefore describe the share of the analyzed group meeting the definition at the assessment time; they do not describe the amount of function restored or the duration of restored function.

The specified assessment time matters to interpretation. This endpoint concerns restoration 120 minutes after the first dose, rather than the earlier assessment or the outcomes following later administrations. Those are separate secondary outcomes. The primary analysis population is identified as modified intent to treat, but the registry record does not report the detailed inclusion rules for that population or how unavailable endpoint assessments were handled.

7. Results Posted in the Registry

• Tenecteplase + Tenecteplase + Placebo (TTP): 60.0% (30/50) versus 23.4% (11/47) on control; risk difference 36.6 percentage points (95% CI 18.4 to 54.8), risk ratio 2.56 (1.46–4.51); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Patients Who Had Restoration of CVC Function Following a Single Administration of Study Drug

• 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:
  • Tenecteplase + Tenecteplase + Placebo (TTP): 22.0% (11/50) versus 10.6% (5/47) on control; risk difference 11.4 percentage points (95% CI -3.1 to 25.8), risk ratio 2.07 (0.78–5.51); unadjusted two-proportion z-test p = 0.132.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tenecteplase + Tenecteplase + Placebo (TTP) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Patients Who Had Restoration of CVC Function Following a Second Administration of Study Drug

• 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:
  • Tenecteplase + Tenecteplase + Placebo (TTP): 70.0% (35/50) versus 42.6% (20/47) on control; risk difference 27.4 percentage points (95% CI 8.4 to 46.5), risk ratio 1.64 (1.13–2.40); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tenecteplase + Tenecteplase + Placebo (TTP) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Patients Who Had Restoration of CVC Function Following a Third Administration of Study Drug

• 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:
  • Tenecteplase + Tenecteplase + Placebo (TTP): 88.0% (44/50) versus 83.0% (39/47) on control; risk difference 5.0 percentage points (95% CI -9.0 to 19.0), risk ratio 1.06 (0.90–1.25); unadjusted two-proportion z-test p = 0.482.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tenecteplase + Tenecteplase + Placebo (TTP) and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the registry presents a changing pattern across assessment times and administrations. The results are not uniform: the group contrast is less clear at the early assessment, more separated at the second-administration assessment, and closer at the third-administration assessment. This broad pattern is compatible with the primary result showing a difference at its specified time, but the secondary endpoints address different moments and treatment sequences rather than repeating the primary question.

Secondary outcomes can help describe the course of observed catheter restoration, but they should not be treated as interchangeable with the primary endpoint. Each has its own assessment time and, where relevant, follows a further administration. A percentage at one point in the treatment sequence does not by itself establish what caused a later change or whether patients with restoration at one assessment remained restored at another.

The registry lists several secondary outcome measures and multiple analyses, but a plan for controlling the chance of false-positive findings across these outcomes is not reported in the registry record. When many outcomes are examined, some may appear statistically notable by chance even if there is no underlying difference. For that reason, unadjusted secondary results carry less confirmatory weight than the prespecified primary comparison. They are best read as descriptive or supportive evidence unless an appropriate analysis plan and multiplicity handling are available.

The secondary findings do not overturn the primary result, nor do they independently establish a broader treatment effect. Their contribution is to show that the observed group contrast depends on the endpoint timing and administration stage. Interpretation should keep those distinctions visible and avoid selecting a single secondary result as definitive without the missing analysis-plan context.

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

• Percentage of Patients Who Had Restoration of CVC Function Following a Single Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Single Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Second Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Second Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Second Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Third Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Third Administration of Study Drug
• Percentage of Patients Who Had Restoration of CVC Function Following a Third Administration of Study Drug

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: the registry records the percentage of participants who met a defined restoration criterion. For such outcomes, a group percentage is the proportion of analyzed participants with the event. A contrast between percentages can be expressed as a risk difference, which describes the absolute separation between the group proportions. The recalculated risk difference is an unadjusted comparison based on the posted summary counts and group sizes.

What does the confidence interval describe?

A confidence interval gives a range of values compatible with the observed data under the assumptions of the estimation method. It communicates uncertainty about the estimated contrast, not a range containing a stated percentage of individual patient outcomes. A narrower interval indicates greater precision, while a wider interval indicates greater uncertainty. The interval does not account automatically for every possible source of bias, such as outcome misclassification or missing data.

How should the p-value be read?

A p-value describes how unusual data at least as discordant with a specified no-difference model would be, assuming that model and the analysis assumptions are correct. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. The registry reports a Cochran-Mantel-Haenszel analysis for the primary comparison. The registry record does not give the detailed implementation or any strata used, so those details should not be inferred from the method name alone.

Why distinguish the sponsor analysis from the recalculation?

The sponsor-reported analysis is the trial analysis recorded by the registry. The recalculated comparison is a simple, unadjusted re-analysis from the posted group summary statistics. It is useful as a transparent check on the direction and approximate magnitude of the contrast, but it is not a replacement for the sponsor's analysis, which may use analytic details not recoverable from the summary figures. In this case, the sponsor-reported result and the recalculated result are broadly consistent in direction and size. The registry does not identify a discrepancy.

What does randomization contribute?

Random assignment aims to make the treatment groups comparable at the start of a trial, including with respect to characteristics that are measured and those that are not. Double blinding is intended to reduce the influence of treatment knowledge on participant experience and assessment. These design features support a causal interpretation of a between-group contrast when implementation and follow-up are sound, but they do not remove all uncertainty. The registry record does not report the randomization sequence-generation method, concealment procedures, or details of masking.

What is the role of the analysis population?

The primary outcome is identified as using a modified intent-to-treat population. An analysis population defines which randomized participants contribute to a particular result. The term alone does not reveal the exact eligibility or evaluability rules used in this trial. Those rules, including the treatment of participants without an assessment, are not reported in the registry record. The posted outcome group sizes should therefore be interpreted as the analyzed group sizes for this endpoint, not as a complete account of participant flow.

Why can later assessments differ from the primary endpoint?

The secondary outcomes assess restoration at other times and after additional administrations. The event proportion at an earlier assessment need not match the proportion at a later assessment, because the assessment time and study-drug administration differ. These outcomes answer related but distinct questions. Their results do not change the definition of the primary endpoint, and the methods for combining or adjusting across the multiple outcome assessments are not reported in the registry record.

All statistical interpretations depend on the quality and completeness of outcome measurement, the comparability of the randomized groups, and the suitability of the analysis. A statistical method can quantify sampling uncertainty under its assumptions, but it cannot correct for information that is not reported or establish the clinical importance of a measured difference.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a mean difference of 36.6 percentage points, with a 95% confidence interval from 18.4 to 54.8. The unadjusted recalculation reports a risk difference of 0.366, with a 95% confidence interval from 0.184 to 0.548. The measures use different scales: the sponsor result is stated in percentage points, while the recalculation expresses the difference as a proportion. Both intervals remain on the positive side of no difference, and both indicate uncertainty about the exact size of the contrast.

A confidence interval is not a guarantee that the true effect lies within its endpoints. It is a measure of statistical uncertainty under the analysis assumptions. The interval does not capture possible selection, measurement, or reporting biases, and the registry record does not provide enough detail to evaluate all such issues.

The primary endpoint group sizes are 47 and 50. Precision depends in part on the amount of information in the analyzed groups and on the frequency of the outcome. The posted interval provides a more complete sense of precision than the point estimate alone: while the point estimate gives a single summary, the interval shows that a range of effect magnitudes remains compatible with the data. The reported interval is appreciably bounded away from no difference, but its width also means the exact magnitude is not pinned down to a single value.

For the recalculation, the interval is based on an unadjusted approach using the posted summary data. The sponsor analysis uses the Cochran-Mantel-Haenszel method. Their slightly different reported endpoints reflect distinct analysis presentations and rounding; the registry record does not identify a discrepancy. The sponsor analysis remains the trial's reported result, while the recalculation offers a simple supplementary estimate.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations based on the observed effect, not the trial's original design assumptions. For these binary outcomes, the figures are participants per arm. They are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider effects equal to the observed effect and smaller fractions of that effect.

The 80% power column gives the planned number of participants per arm under those assumptions for an analysis with an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column gives the corresponding planning target for a 90% chance. Higher planned power generally requires more participants for the same effect and assumptions. Smaller effects are harder to distinguish from chance variation, so the illustrations require more participants per arm when the assumed effect is a smaller fraction of the observed effect.

These values are not observed power. They are planning illustrations derived from the observed effect and stated assumptions; they do not describe the probability that the completed trial detected an effect. The trial's own original sample-size assumptions and justification are not reported in the registry record. The calculations should therefore be read as conditional examples of how sample-size needs change with a chosen effect size and power target, rather than as evidence about the design process used for this trial.

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 = 0.234; treatment proportion p₁ = 0.600; average p̄ = 0.417.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6973 = 1.3667.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6475 = 0.5450.
4. n = (1.3667 + 0.5450)² / (0.3660)² = 27.3, rounded up to 28 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 <- 0.234042553191489                          # control proportion
p1 <- 0.6                          # 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(395876)
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 = 28 (80% power), 37 (90% power)
 75% of observed effect: n per arm = 48 (80% power), 64 (90% power)
 50% of observed effect: n per arm = 102 (80% power), 136 (90% power)
power.prop.test: 27.3 
Simulated power at n = 28 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

The sponsor-reported primary analysis uses the Cochran-Mantel-Haenszel method and gives a mean difference of 36.6, with a 95% confidence interval from 18.4 to 54.8 and p < 0.001. This is the analysis recorded by the trial and is the appropriate primary reported result to cite. The registry record does not provide further implementation details for the method.

The simple recalculation from the posted summary statistics gives a risk difference of 0.366, with a 95% confidence interval from 0.184 to 0.548 and p < 0.001. It is unadjusted and uses the available group summaries; it may not reproduce details of the sponsor's analysis. The measures are reported on different scales, and the values should be interpreted accordingly rather than as competing estimates of different outcomes.

The sponsor result and recalculation tell a consistent broad story about the primary comparison: both estimate a higher restoration proportion in the group assigned tenecteplase as the initial study drug, and both intervals exclude no difference. The registry does not flag a discrepancy. The recalculation is a check on the summary data, not a substitute for the reported trial analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and lists secondary outcome measures, including assessments following first, second, and third administrations. It does not report whether the trial used a prespecified hierarchy, an adjustment for multiple comparisons, or another multiplicity strategy. Without that information, the secondary p-values should not be read as if each were the sole planned test. Examining multiple outcomes can raise the chance of at least one apparently positive result by chance, which is why unadjusted secondary evidence warrants caution.

The primary result is distinct from this concern because it is identified as the primary outcome and has a reported sponsor analysis. The registry record does not give enough detail to determine whether other planned analyses or interim looks were conducted; interim analyses and stopping rules are not reported in the registry record. No assumptions about them should be made.

The endpoint population is identified as modified intent to treat, but the registry record does not state the detailed rules defining that population. The posted group sizes for the primary endpoint are 47 and 50, while the enrollment figure is 100. The reason for this difference, participant disposition, and the handling of missing or unevaluable outcomes are not reported in the registry record. It is therefore not possible to assess from this record alone whether missing observations could have affected the group comparison or how robust the result is to alternative missing-data assumptions.

The record also does not report whether the analysis was adjusted for baseline factors, how any stratification was handled, or the full statistical analysis plan. The reported method name does not supply those details. These omissions do not negate the posted result, but they limit independent assessment of analytic choices, multiplicity control, and the relationship between the analyzed population and all randomized participants.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: mental status changes (2.1%), pancytopenia (2.0%), venous thrombosis (2.0%).

The registry reports serious adverse events for the two sequence groups. In the PTT group, 1 serious adverse event is recorded among 47 at risk; in the TTP group, 2 are recorded among 50 at risk. These are event counts, not estimates of whether one sequence is safer than the other. The registry record does not provide enough detail about event timing, relationship to study drug, or the full criteria used for attribution.

Other adverse events are listed as 6 among 47 at risk in the PTT group and 14 among 50 at risk in the TTP group. The record also lists Mental Status Changes at 2.1%, Pancytopenia at 2.0%, and Venous Thrombosis at 2.0% among the top serious adverse-event terms. The registry record does not clarify the denominators or group attribution for those listed term percentages, so they should not be used to infer group-specific rates.

Deaths are not reported in the registry record. Adverse-event counts from this trial are descriptive; they do not by themselves establish a causal relationship or provide a complete comparison of safety. The record's safety information should be interpreted alongside its limited reporting detail and the group sizes involved.

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

The primary result describes the proportion of patients meeting a specific definition of catheter-function restoration at a stated assessment time. In this randomized comparison, that proportion was higher in the group assigned tenecteplase as the initial study drug than in the group assigned placebo initially. The sponsor-reported analysis and the unadjusted recalculation are consistent in the direction of that difference, and their confidence intervals exclude no difference.

This does not mean that every patient experienced restoration, that function remained restored, or that all catheter-related problems were resolved. The endpoint records whether the stated withdrawal and infusion criteria were met at the assessment. It does not measure duration, degree of restored function, or every aspect of clinical benefit.

The result also does not establish that the same contrast would occur in every setting or population. The trial enrolled adult and pediatric patients at centers in the United States and Canada, but the registry record does not provide detailed subgroup results or enough information to assess how the findings vary across patient characteristics. Generalization beyond the studied setting requires evidence beyond this endpoint comparison.

A statistical difference is not the same as a complete account of clinical importance. The estimated difference and its confidence interval describe the measured outcome and uncertainty; they do not determine how meaningful the outcome is to patients or clinicians. Safety information is limited in the registry record, and the primary result should not be taken as a comprehensive assessment of benefit and harm.

Finally, the result should be distinguished from the secondary outcomes. Later assessments and additional administrations address different questions, and no multiplicity plan is reported. The primary comparison is the clearest confirmatory result in the record; secondary findings add context but do not independently settle the broader interpretation.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical question becomes a statistical endpoint. Catheter restoration is defined through explicit withdrawal and infusion criteria, then summarized as the percentage meeting those criteria at a specified time. That makes the outcome interpretable as a binary event while also showing why the assessment time and operational definition matter.

It also demonstrates the value of reading a point estimate together with its interval and the analysis method. The sponsor's reported Cochran-Mantel-Haenszel result and a simple unadjusted recalculation are not identical presentations, but they give a consistent broad account of the primary contrast. The sponsor analysis is the trial-reported analysis; the recalculation helps readers understand the summary data without implying that it reproduces every analytic detail.

The trial further highlights the distinction between a primary endpoint and multiple secondary assessments. Outcomes at different stages of administration can show different patterns, and multiplicity matters when interpreting a collection of unadjusted tests. A result that is statistically persuasive for the primary question does not automatically validate every related secondary comparison.

Finally, the record shows why transparent reporting matters. Details about analysis populations, missing data, multiplicity, and the original sample-size rationale affect how confidently readers can evaluate the evidence. Their absence does not erase the reported primary finding, but it limits the depth of independent statistical appraisal.

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 posted outcome group sizes differ from the enrollment figure, and the registry record does not explain the difference or provide a participant-flow account. Although the primary endpoint population is labeled modified intent to treat, its detailed inclusion rules are not reported. The handling of missing or unevaluable outcome data is also not reported in the registry record, limiting assessment of potential bias from incomplete follow-up.

The record gives the primary method name but not the details needed to reproduce the sponsor analysis, such as any strata or covariate handling. It does not report the original sample-size justification, the multiplicity strategy, or whether interim analyses were conducted. These gaps are particularly relevant when assessing secondary results and the planning context for the trial.

The arm descriptions are blank, while the arm titles describe multi-administration sequences. The brief summary clarifies the randomized initial dose, but fuller dosing and procedural details are not reported in the registry record. The primary endpoint concerns a single administration, so interpretation should not extend it to unreported details of later treatment procedures.

Safety reporting is also limited. The registry provides serious and other adverse-event counts, but the record does not report deaths and does not give enough detail to establish attribution or interpret the listed serious-event term percentages by group. The available safety information therefore cannot serve as a complete comparative safety assessment.

These are limitations of the registry record and the posted summaries. They do not demonstrate that the trial was conducted improperly; they identify aspects that cannot be assessed from the reported information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Tenecteplase for Restoration of Function in Dysfunctional Central Venous Catheters — NCT00395876.
• Registry record last updated 2010-08-10; status last verified 2010-07.
• Results first posted 2010-08-10.
• 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 Phase III, randomized, double-blind, placebo-controlled, parallel-group study of tenecteplase for dysfunctional central venous catheters. It reports enrollment of 100 adult and pediatric patients and conduct at 24 centers in the United States and Canada. The primary endpoint was restoration of catheter function 120 minutes after the first dose, in the modified intent-to-treat population.

Restoration was reported for 23.4% of the PTT group and 60.0% of the TTP group. The sponsor analysis reported a mean difference of 36.6, with a 95% confidence interval from 18.4 to 54.8 and p < 0.001. The unadjusted recalculation was consistent in direction. Details about missing data, multiplicity, and the original design assumptions are not reported in the registry record.