Ethanol Lock Therapy for Treatment and Secondary Prophylaxis of Central Line-Associated Bloodstream Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ethanol Lock Therapy for Treatment and Secondary Prophylaxis of Central Line-Associated Bloodstream Infection (NCT01472965), a randomized phase 3 study. The primary outcome is Percentage of Therapeutic Failures (Early or Late Failure) in Children and Adolescents With CLABSI Receiving Standard Care Plus Ethanol Lock Therapy (ELT) vs. Standard Care Alone.

2. Clinical Question

The clinical question focuses on both initial treatment and prevention of subsequent infection. Therapeutic failure was defined as a composite: it could occur during the treatment phase through early failure, or during the prophylaxis phase through relapse or reinfection. The outcome therefore represents a broader course of infection-related events, rather than a measure of clearance alone.

The registry describes the rationale as a concern that infection may persist or recur after treatment and that another line infection may follow an earlier one. The trial tested whether adding ethanol lock therapy to standard care could reduce the risk of the composite outcome in this pediatric population. The primary result does not by itself answer whether ELT affects each component separately; component outcomes are listed as secondary outcomes and have their own reported estimates.

3. Trial Design

The registry describes a phase 3, randomized, quadruple-masked, parallel-group trial. The treatment group received standard care plus ethanol lock therapy, and the control group received standard care with a heparin-saline placebo catheter lock. The enrollment recorded in the registry is 95. The primary outcome results list 48 participants in the ethanol group and 46 in the placebo group; these endpoint denominators should be read as the denominators reported for those results, not as a reconciliation of enrollment and analysis populations.

Eligible patients had CLABSI and were being treated for cancer or hematologic disorders, or undergoing hematopoietic stem cell transplantation. The arm descriptions state that enrollment was to occur within 96 hours of collection of a positive blood culture. The trial was conducted by St. Jude Children's Research Hospital and is recorded as completed. The registry dates are 2011-12-29 for study start and 2016-11-11 for primary completion.

The intervention involved catheter lock therapy rather than a comparison of the groups' standard infection care. The registry describes ELT as a solution of ethanol and water placed into a line or port, left to dwell for 2 hours, and withdrawn. The treatment arm description specifies 70% ethanol. The placebo was heparin-saline. Because allocation was randomized and masking was recorded as quadruple, assignment was intended to support a fair comparison while limiting knowledge of treatment assignment. The identities of all masked roles are not reported in the registry record.

The primary outcome was assessed up to 25 weeks after treatment began. The definition divided that period into a 5 day treatment phase for early failure and a 24 week prophylaxis phase for late failure. The registry does not report the original sample-size justification, the detailed randomization procedure, or the trial's statistical analysis plan. Those omissions limit assessment of how the planned design related to the final analysis.

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

Reasons for not completing this period:

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 Therapeutic Failures (Early or Late Failure) in Children and Adolescents With CLABSI Receiving Standard Care Plus Ethanol Lock Therapy (ELT) vs. Standard Care Alone, measured over Up to 25 weeks after the start of treatment..

The primary endpoint was the percentage of evaluable participants with therapeutic failure, assessed up to 25 weeks after the start of treatment. It was a composite outcome designed to capture failure during initial treatment as well as subsequent infection-related failure during prophylaxis. The registry defined early failure as central line removal, death, persistent positive blood cultures for >72 hours, development of new CLABSI, or initiation of other ALT during the 5 day treatment phase. Late failure was relapse, defined as new CLABSI with an identical organism, or reinfection, defined as new CLABSI with a different organism, during the 24 week prophylaxis phase.

A composite can represent several clinically relevant ways that the treatment course may fail, and can capture more events than any single component alone. Its interpretation depends on the components: an observed difference in the composite could reflect one or more components, and the composite does not show which component drove the result. The registry reports relapse and reinfection separately as secondary outcomes, but the primary result combines early and late failure.

The primary endpoint is reported as a percentage of participants, rather than as a time-to-event measure or a continuous measurement. The percentage describes the proportion of evaluable participants who met the composite definition during the stated follow-up period. The registry does not report further detail on the evaluability criteria or how incomplete follow-up was handled.

7. Results Posted in the Registry

• Treatment (Ethanol): 43.8% (21/48) versus 43.5% (20/46) on control; risk difference 0.3 percentage points (95% CI -19.8 to 20.3), risk ratio 1.01 (0.64–1.59); unadjusted two-proportion z-test p = 0.979.

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.

Cumulative Incidence of Therapeutic Failure in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone

• 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:
  • Treatment (Ethanol): 43.8% (21/48) versus 43.5% (20/46) on control; risk difference 0.3 percentage points (95% CI -19.8 to 20.3), risk ratio 1.01 (0.64–1.59); unadjusted two-proportion z-test p = 0.979.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment (Ethanol) and the control. The interval gives the range of effects that remain compatible with the data.

Cumulative Incidence of Relapse in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone

• 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:
  • Treatment (Ethanol): 6.2% (3/48) versus 8.7% (4/46) on control; risk difference -2.4 percentage points (95% CI -13.1 to 8.2), risk ratio 0.72 (0.17–3.04); unadjusted two-proportion z-test p = 0.652.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment (Ethanol) and the control. The interval gives the range of effects that remain compatible with the data.

Cumulative Incidence of Reinfection in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone

• 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:
  • Treatment (Ethanol): 27.1% (13/48) versus 23.9% (11/46) on control; risk difference 3.2 percentage points (95% CI -14.4 to 20.8), risk ratio 1.13 (0.57–2.27); unadjusted two-proportion z-test p = 0.725.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment (Ethanol) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question by separating relapse and reinfection and by listing therapeutic failure, catheter occlusion events, and adverse events. This gives a broader view of the types of events considered in the trial, while the primary composite remains the main registered endpoint. The detailed secondary results do not present a uniformly different pattern from the primary comparison: the component estimates vary in direction, and their uncertainty is substantial.

Those component outcomes are related to, but not interchangeable with, the primary result. Relapse and reinfection form parts of late failure in the composite definition, whereas early failure includes other events during the treatment phase. Separate results can help identify which kinds of events contribute to the overall clinical picture, but event-specific estimates may be based on fewer observed events and can be less precise. The individual secondary estimates should therefore be considered alongside, not instead of, the primary composite result.

The registry lists five secondary outcomes, including measures of occlusion and adverse events, but not all listed outcomes have detailed numeric results in the posted outcome data. Reported analyses are not listed. The registry record does not report whether secondary comparisons were prespecified as confirmatory or exploratory, or whether multiplicity adjustments were planned.

When several outcomes are examined, the chance of finding an apparently notable result by chance can increase. Unadjusted secondary results therefore carry less weight than a prespecified primary comparison, especially when there is no reported plan for controlling the overall error rate. This does not make the secondary findings irrelevant; it means they are best treated as descriptive evidence that can inform further study, rather than as independent proof of a treatment effect.

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

• Cumulative Incidence of Therapeutic Failure in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone
• Cumulative Incidence of Relapse in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone
• Cumulative Incidence of Reinfection in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone
• Rate of Central Venous Access Device (CVAD) Occlusion Events in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone
• Adverse Events in Participants Receiving Standard Care Plus ELT vs. Standard Care Alone

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference subtracts the event percentage in a reference group from the event percentage in the group of interest. In this comparison, the reported contrast is oriented as ethanol minus placebo. A positive value means the event percentage was higher in the ethanol group in the observed data; a negative value means it was lower. The primary estimate is 0.003, corresponding to the small separation between the reported group percentages. The direction of this arithmetic contrast does not by itself establish a treatment effect.

A risk difference is an absolute measure: it describes the difference in event probability, not the relative proportion of events between groups. It is often straightforward to interpret because it uses the same scale as the endpoint. Here, the endpoint is a percentage of participants with the composite event. The confidence interval around the risk difference shows how much uncertainty remains around the estimated contrast.

Why does the endpoint definition matter?

The primary result uses a composite outcome, with several qualifying events. Composite outcomes can summarize a range of ways a treatment course may fail and can be useful when each component is relevant to the trial question. However, the components may differ in frequency or clinical meaning. A single composite estimate cannot reveal whether the groups differed on one component, several components, or none individually. Separate component results may help describe the pattern, but they are not automatically as reliable or definitive as the primary outcome.

In this trial, the definition distinguishes early events during the 5 day treatment phase from relapse or reinfection during the 24 week prophylaxis phase. The outcome therefore brings together events occurring in different parts of follow-up. It is important to retain that definition when interpreting the overall percentage: it is not simply a count of recurrent infections, nor is it limited to failure to clear the initial infection.

What does the p-value say?

The unadjusted p-value is 0.979. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not measure the probability that a result will replicate. A large p-value does not show that the groups are equivalent. The registry does not report a prespecified equivalence margin or a noninferiority objective.

The posted comparison is described as an unadjusted recalculation from the group summaries. The registry record contains no reported analyses, so the statistical test used for a sponsor's primary analysis and its adjustment procedures are not reported in the registry record. The recalculated result provides a way to describe the posted summaries, not a replacement for an analysis specified by the trial investigators.

How should the confidence interval be read?

A confidence interval gives a range of values that are reasonably compatible with the observed data under the method used to calculate it. In repeated use of a method under its assumptions, intervals at a stated confidence level have a long-run coverage interpretation. For an individual trial, the interval does not assign a probability to the true effect being within its particular endpoints. It also does not account automatically for all possible biases, missing data, or departures from the analysis assumptions.

The interval for the primary risk difference crosses zero. Zero corresponds to no difference on the risk-difference scale. Values on either side remain compatible with the data, so the result does not precisely determine whether the event percentage is lower or higher with ethanol. The interval's width is also important: it signals that effects of materially different directions and sizes remain plausible under the recalculation.

Why can event counts affect precision?

For binary outcomes, the amount of information depends on the number of participants and how many experience the event, as well as the statistical method. When relatively few events inform a comparison, estimates can be imprecise even when the reported percentages appear similar. More information can narrow uncertainty, but increasing sample size alone does not correct bias, inconsistent outcome ascertainment, or other design problems.

General statistical context: the event counts and denominators are the basis for estimating the group percentages and their contrast. The analysis should also account for the endpoint's evaluable population and follow-up. The registry reports group denominators for the outcome but does not report the evaluability rules or missing-data procedures in detail. The posted summaries therefore do not permit a full assessment of how incomplete outcome data may have affected the estimate.

What can be inferred from this comparison?

Random allocation is a design feature intended to make the groups comparable on average, including with respect to factors that may not have been measured. Masking can help reduce differences in care or assessment that arise when assignment is known. These protections support interpretation, but they do not guarantee that every source of bias is absent. The registry record does not provide enough detail to evaluate the allocation sequence, concealment procedures, or the success of masking.

The trial's result concerns the assigned catheter-lock strategies in the registered population and follow-up. It does not isolate the effect of ethanol from every aspect of care beyond the randomized comparison, and it cannot establish the result for unrepresented populations or different protocols. Interpretation also depends on adherence, outcome assessment, and analysis choices, details of which are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.003, with a 95% confidence interval from -0.198 to 0.203. The interval crosses zero and spans values in both directions. Thus, the data are compatible with an event percentage lower in the ethanol group and also with an event percentage higher in that group. The point estimate alone is close to zero, but it should not be read as a precise estimate of no difference because the interval is wide.

For context, the posted endpoint percentages are 43.8% for ethanol and 43.5% for placebo. Their closeness describes the observed sample, while the confidence interval describes uncertainty about the underlying contrast. These are different pieces of information: similar observed percentages do not guarantee that the true difference is small, particularly when the interval includes effects in both directions.

The interval is based on an unadjusted recalculation from the posted summary statistics. It does not reflect uncertainty about unreported analysis decisions, possible missing outcomes, or the generalizability of the trial beyond its registered population. No confidence intervals for the group percentages themselves are reported in the registry record. The reported ratio estimates also have broad intervals, consistent with limited precision in the comparison, and should be interpreted as supporting context rather than as a separate primary conclusion.

Precision is not the same as clinical importance. Deciding whether a range of effects would matter requires a prespecified clinical context or threshold, which is not reported in the registry record. The result therefore identifies uncertainty in the estimated contrast but does not establish a threshold for benefit or harm.

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 figures are planning illustrations derived from the observed effect, not the original trial design calculation. They are expressed as participants per arm for 80% power and participants per arm for 90% power. The 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 at the stated fraction of the observed effect.

The 80% power column represents the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect at the stated significance level, if the assumptions hold. The 90% power column gives the corresponding planning target for a higher chance of detecting that same effect. These are design calculations for a hypothetical future study, not estimates of what happened in this trial.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the target changes when the effect to be detected is smaller than the observed estimate. Smaller effects generally require more participants to distinguish them from no difference with the same planned power and significance level. The very large planning figures for the primary comparison reflect the small observed risk difference used in this illustration; they should not be treated as recommended enrollment targets without considering a clinically meaningful effect and an appropriate design.

This is not observed power. Observed power calculated from the result would not clarify the uncertainty better than the estimate and its confidence interval. The sample-size display is a planning aid based on stated assumptions, and the trial's own original design assumptions and sample-size justification are not reported in the registry record.

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 = 0.435; treatment proportion p₁ = 0.438; average p̄ = 0.436.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7013 = 1.3746.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7013 = 0.5902.
4. n = (1.3746 + 0.5902)² / (0.0027)² = 522,793.1, rounded up to 522,794 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 <- 0.434782608695652                          # control proportion
p1 <- 0.4375                          # 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(1472965)
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 = 522,794 (80% power), 699,872 (90% power)
 75% of observed effect: n per arm = 929,247 (80% power), 1,243,997 (90% power)
 50% of observed effect: n per arm = 2,090,435 (80% power), 2,798,498 (90% power)
power.prop.test: 522793.1 
Simulated power at n = 522,794 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, time points, subgroups, or comparisons. If each is assessed without adjustment, the overall chance of at least one apparently unusual result can be greater than the chance associated with any single test. The registry lists a primary composite and several secondary outcomes, but the registry record does not report a multiplicity strategy, such as a hierarchy of tests or an adjustment to the significance threshold. It also does not report whether secondary outcomes were intended to support confirmatory conclusions or to describe additional aspects of the trial.

The record lists no reported analyses. It therefore does not state the statistical model or test used for the primary analysis, whether any covariates were included, or how repeated or related outcomes were handled. The unadjusted comparisons described for the posted summaries should be read as recalculations, not as evidence about the original prespecified analysis procedure.

Missing-data handling is also not reported in detail. The primary result is described as a percentage of evaluable participants, and the outcome arms have reported denominators. However, the registry does not define evaluability, describe the amount or reasons for missing outcome data, or specify whether participants were analyzed according to their randomized assignment. Without those details, it is not possible to assess how exclusions or incomplete follow-up may have influenced the estimate.

Analysis populations are not described in the registry record. The distinction between all randomized participants, participants who received assigned treatment, and participants with evaluable outcome data can matter, particularly when treatment discontinuation or missing assessments occur. No such analysis sets or sensitivity analyses are reported. These gaps constrain assessment of robustness and should be kept separate from the numerical uncertainty represented by the confidence interval.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: line fracture or split (12.5%), dyspnea (2.2%).

The registry reports serious adverse event figures for 48 participants in the ethanol group and 46 in the placebo group. Serious adverse events affected 6 participants in the ethanol group and 5 in the placebo group. Other adverse events affected 4 participants in the ethanol group and 0 in the placebo group. Deaths were reported for 3 participants in the ethanol group and 4 in the placebo group. These are descriptive counts in the record; they do not by themselves establish that an event was caused by the assigned catheter lock.

The listed top serious adverse event terms are “Line fracture or split” at 12.5% and “Dyspnea” at 2.2%. The record does not provide the arm attribution for these terms in the listed summary, so they should not be assigned to a treatment group on that basis. Nor does the summary provide enough detail to assess timing, severity beyond the serious-event classification, relatedness, or how overlapping events were counted.

Safety comparisons need caution because the registry does not report inferential analyses for these figures. The counts describe events recorded during the trial and should be interpreted alongside the population, follow-up, and incomplete reporting details. They are not a standalone measure of overall safety or a causal comparison.

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

The posted primary results show nearly identical observed percentages of therapeutic failure in the two groups: 43.8% with ethanol and 43.5% with placebo. The recalculated unadjusted risk difference is small, and its confidence interval includes values in both directions. The result therefore does not provide a precise answer about whether adding ethanol lock therapy changes the risk of the defined composite outcome in the studied population.

This is not the same as demonstrating that the strategies are equivalent. Equivalence requires a prespecified margin defining how much difference would be considered acceptably small, together with an analysis designed to assess that question. The registry does not report such a margin or an equivalence analysis. Likewise, the result does not establish that ethanol is beneficial or harmful. It describes the available comparison and its uncertainty.

The outcome also has a specific scope. It combines early treatment failure with relapse and reinfection during the prophylaxis phase, and it covers follow-up up to 25 weeks after treatment began. It does not directly answer whether ELT changes every component individually, whether it affects outcomes beyond the recorded follow-up, or whether it has the same relationship with outcomes in other clinical populations.

Randomization and masking are relevant strengths of the registered design, but interpretation remains dependent on the details of conduct and analysis. The registry does not report the original sample-size justification, detailed analysis plan, missing-data methods, or analysis populations. These omissions do not change the posted numbers, but they limit assessment of how robustly the trial addresses its question.

For clinical researchers, the most defensible reading is descriptive: the observed primary percentages were close, while the interval around their difference remains broad. The secondary outcomes and safety counts add context but do not remove the uncertainty in the primary result. The findings should not be generalized beyond the recorded population and treatment comparison without additional evidence.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a p-value are not enough to characterize a clinical comparison. The observed primary percentages are close and the unadjusted p-value is 0.979, but neither fact establishes equivalence. The confidence interval is essential because it displays the range of effects still compatible with the data and makes the remaining uncertainty visible.

It also shows how composite endpoints simplify a complex course of illness while requiring careful interpretation. Combining early failure, relapse, and reinfection can capture several meaningful ways a treatment strategy may fall short. At the same time, an overall composite percentage cannot identify which component accounts for the result. Separate component outcomes add detail, but they may be less precise and are subject to the interpretive cautions that apply to multiple secondary comparisons.

The planning illustration is another useful statistical distinction. Sample-size figures based on an observed effect are not evidence of the trial's power after the fact, and they are not the trial's original design assumptions. They show how planning requirements can change when the effect targeted becomes smaller. A future design would need a clinically meaningful target and a prespecified analysis plan rather than relying only on the observed estimate.

Finally, the record highlights the value of transparent reporting. Information about analysis populations, missing data, multiplicity, and the original statistical plan is needed to evaluate how estimates were produced and how robust they are. The reported randomized and masked design supports a structured comparison, while the limitations in the registry record set boundaries on what can be concluded statistically.

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

The confidence interval for the primary comparison is broad and includes effects in both directions, so the result is not precise enough to determine the direction of the underlying difference. The primary outcome is a composite of early failure, relapse, and reinfection; the overall estimate does not indicate which component contributes most to the result. Component outcomes may be based on fewer events and are less suitable for strong conclusions when considered separately.

The registry record does not report the original sample-size justification or the trial's prespecified statistical analysis plan. It also does not report the analysis populations, detailed evaluability criteria, missing-data procedures, or sensitivity analyses. These gaps prevent a full assessment of whether the posted denominators reflect all randomized participants and whether incomplete follow-up could affect the estimates.

Although the design is recorded as randomized and quadruple-masked, details of sequence generation, allocation concealment, masking roles, adherence, and unmasking are not reported in the registry record. The record also does not explain the analysis of secondary endpoints or how multiple comparisons were handled. Secondary estimates should consequently be viewed as descriptive rather than as a set of confirmatory tests.

The results are specific to the pediatric population and treatment setting described, the catheter-lock strategies compared, and follow-up up to 25 weeks after treatment began. The registry summary does not support conclusions about other populations, treatment protocols, or longer follow-up. Safety reporting is also limited: the summary provides group counts and top serious-event terms, but not the detail needed to assess timing, relatedness, or arm attribution for those terms.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Ethanol Lock Therapy for Treatment and Secondary Prophylaxis of Central Line-Associated Bloodstream Infection — NCT01472965.
• Registry record last updated 2017-11-13; status last verified 2017-08.
• Results first posted 2017-11-13.
• 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 registry describes a completed phase 3 randomized, quadruple-masked, parallel-group trial of ethanol lock therapy for children and adolescents with central line-associated bloodstream infection. The comparison was standard care plus ethanol lock therapy versus standard care with heparin-saline placebo catheter lock therapy. Enrollment is recorded as 95.

The primary endpoint was the percentage of evaluable participants with early or late therapeutic failure up to 25 weeks after treatment began. The posted percentages were 43.8% for ethanol and 43.5% for placebo. The recalculated unadjusted risk difference was 0.003, with a 95% confidence interval from -0.198 to 0.203 and an unadjusted p-value of 0.979. The interval includes differences in both directions and leaves substantial uncertainty.

The registry lists secondary outcomes involving therapeutic failure, relapse, reinfection, catheter occlusion, and adverse events. It does not report the original sample-size justification, detailed analysis plan, missing-data methods, or analysis populations.