Maintaining Patency in Implanted Port Catheters: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Maintaining Patency in Implanted Port Catheters (NCT02354118), a randomized na study. The primary outcome is Number of Participants With First Complete Occlusion Within 1 Year.

2. Clinical Question

The study’s stated purpose was to compare complication rates associated with the two flushing approaches and to identify a flushing solution for maintaining port patency. The registry record describes the comparison, but it does not establish that every potential complication was captured in the primary endpoint. The endpoint specifically counts participants with a first complete occlusion during the stated period.

Statistically, the key question is about the difference in observed event risk between randomized groups, not whether either group had no events. The posted primary estimate is a risk difference, so its sign indicates which group had the higher observed risk. Its confidence interval describes the range of effects compatible with the data under the analysis used. The interval is wide enough to include differences in either direction, so the primary estimate does not precisely determine the direction or size of a group difference.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Participants were assigned to a control group using heparinized saline or an intervention group using saline only. The record lists the study phase as NA and the status as completed. It gives an enrollment of 436; the posted outcome results list 222 participants in the control group and 214 in the intervention group for the primary endpoint.

In a randomized design, assignment is intended to make the groups comparable with respect to factors that could affect the outcome. Randomization supports an interpretation of between-group differences as associated with the assigned flushing strategies, subject to issues such as missing outcome data and the analysis population. The registry record does not describe the randomization method, concealment of allocation, or whether analyses followed assigned groups regardless of treatment actually received.

The parallel structure means the two groups were compared over the same general study period rather than one group receiving both flush strategies in sequence. Masking is listed as none, so the record does not describe blinded assignment or outcome assessment. It does not say whether lack of masking affected how occlusion events were assessed or recorded.

The primary outcome timeframe is baseline to 1 year. It counts participants with a first complete occlusion within 1 year, rather than the total number of occlusion events. The secondary occlusion outcome combines complete or partial occlusion within the same stated period. The intervention description does not state how often saline-only flushes were administered, and the registry record does not report the original sample-size justification, detailed trial protocol, or planned statistical analysis procedures.

The primary completion date is 2021-12-11. Dates and status describe the registry record; they do not supply additional detail about participant follow-up, adherence to the flushing schedule, or the timing of individual outcomes.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: NOTE: 1 participant had BOTH a partial occlusion and a complete occlusion. Therefore, when adding information from Outcome Measures 1 and 2 to determine the total number of participants with either complete or partial occlusions in the "Control Group" is correct as 43 (i.e., (5+39 = 44) - 1 participant in both groups = 43 distinct participants)

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 Number of Participants With First Complete Occlusion Within 1 Year, measured over baseline to 1 year.

The primary endpoint counts participants who had a first complete occlusion, described in the registry as a blockage, within 1 year from baseline. It is a binary outcome at the participant level: each participant either met the endpoint during the stated period or did not. The posted group values are counts of participants with the event, alongside the number of participants listed for each group.

This endpoint addresses a direct consequence relevant to the study’s stated purpose of maintaining patency, meaning unobstructed flow, in implanted port catheters. Complete occlusion is a specific and relatively unambiguous event definition compared with a broader measure that includes partial occlusion. Counting participants with a first event also avoids treating repeated occurrences in one person as multiple participants in the primary outcome.

The endpoint does not describe the duration or severity of an occlusion, the number of repeated episodes, or the consequences for individual participants. It also does not capture all possible catheter complications. The registry lists partial-or-complete occlusion and HIT as secondary outcomes, indicating that the primary endpoint is one component of a broader assessment rather than a complete account of all outcomes.

For the comparison, the registry reports the proportion with an event in each group and an unadjusted risk difference. A risk difference expresses the difference between the groups’ event risks in absolute terms. The confidence interval helps show how uncertain that estimated difference is. The choice of an event count is suitable for comparing whether participants experienced the specified outcome during the stated timeframe, but it does not by itself explain why an event occurred or establish the mechanism behind any group difference.

7. Results Posted in the Registry

• Intervention Group: 1.9% (4/214) versus 2.3% (5/222) on control; risk difference -0.4 percentage points (95% CI -3.0 to 2.3), risk ratio 0.83 (0.23–3.05); unadjusted two-proportion z-test p = 0.779.

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 First Complete or Partial Occlusion Within 1 Year

• 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:
  • Intervention Group: 27.6% (59/214) versus 19.4% (43/222) on control; risk difference 8.2 percentage points (95% CI 0.3 to 16.1), risk ratio 1.42 (1.01–2.01); unadjusted two-proportion z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Intervention Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists two secondary outcomes: participants with complete or partial occlusion within 1 year, and participants with HIT within 1 year. Numeric results are posted for the occlusion composite, but a numeric result for HIT is not reported in the registry record. The composite concerns a broader event definition than the primary endpoint, which counts only first complete occlusion.

The overall pattern is not uniform across endpoint definitions. The primary point estimate favors a lower observed risk in the saline-only group, while the composite comparison points toward a higher observed risk in that group. These are not necessarily contradictory because the outcomes include different events and therefore answer different questions. The composite result should not be substituted for the primary result, and the primary result does not summarize every form of occlusion.

The composite result’s unadjusted p-value is 0.043, and its confidence interval for the risk difference lies above zero. Those figures describe the posted comparison, but they do not account for the fact that more than one outcome is listed. The registry does not report a multiplicity adjustment, a hierarchy assigning priority among secondary outcomes, or a prespecified interpretation plan. General statistical principle: testing multiple outcomes without adjustment can make an isolated low p-value less persuasive than a result that was the sole planned primary test.

The record also does not report the analysis for HIT, so the secondary outcome list cannot be treated as a complete set of numerical comparisons. The absence of a posted result does not establish that no HIT events occurred; it means the registry record does not give a numerical comparison for that outcome. In assessing the secondary pattern, the primary endpoint remains the designated main question, while the composite offers additional but less definitive context.

These outcomes should be considered together without averaging them or selecting only the result with the more striking p-value. The difference in endpoint definitions, unadjusted testing, and missing numeric HIT result all limit a broad interpretation. The secondary findings are most useful as context for the primary result and as a reason to recognize uncertainty about the wider range of complications.

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

• Number of Participants With First Complete or Partial Occlusion Within 1 Year
• Number of Participants With HIT Within 1 Year

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant experienced a first complete occlusion within the specified period. For a binary outcome, the event count is considered in relation to the number of participants in the group. The registry reports the corresponding event risks and a risk difference comparing intervention with control. This gives both the event frequency within each group and an absolute-scale estimate of the between-group contrast.

A risk difference is calculated as the intervention-group risk minus the control-group risk. A negative estimate means the observed risk was lower in the intervention group; a positive estimate means it was higher. The primary estimate is -0.004. Its confidence interval ranges from -0.030 to 0.023, so it includes zero and allows effects in either direction. This is a description of the reported estimate and interval, not a new calculation.

The registry also posts a risk ratio and an odds ratio for the primary comparison. These are relative measures: the risk ratio compares the groups’ event risks, while the odds ratio compares their event odds. Relative measures can look numerically different from absolute measures because they use different scales. When events are uncommon, the absolute difference can be small while a relative estimate remains compatible with a broad range of possibilities. The posted intervals for these relative measures are also broad. The record does not identify a single measure as the sole basis for its conclusion.

The reported p-value is unadjusted. In general, a p-value evaluates how incompatible the observed data are with a specified null model, conditional on the assumptions of the test. It is not a measure of the clinical importance of an effect, nor the probability that chance alone caused the result. The registry record does not describe the statistical test, any covariate adjustment, or the precise assumptions used for the posted comparison. Accordingly, the p-value is best read alongside the effect estimate and confidence interval rather than as a complete summary.

Confidence intervals express uncertainty around an estimate under the method used to construct them. In general, a narrower interval indicates greater precision and a wider interval indicates less precision. An interval that crosses zero for a risk difference includes both a no-difference value and values on either side. That does not prove no effect; it shows that the data do not pin down the direction with precision. The primary interval spans negative and positive values, while the secondary composite interval is entirely positive.

For low event counts, estimates can be sensitive to a small number of outcomes. General statistical principle: sparse binary data can produce unstable relative estimates and broad intervals, especially when a group has few events. The primary comparison has only a few events in each group. This makes the confidence interval and the outcome definition particularly important for interpretation. The record does not report a rare-event method, an exact test, or a sensitivity analysis, so no claim about those methods can be made.

The secondary composite endpoint counts participants with a complete or partial occlusion. The primary endpoint is narrower and counts only first complete occlusion. In general, combining event types can increase the number of observed outcomes, but it also changes what the result means: the composite reflects either type, not complete occlusion alone. The primary outcome description notes that one participant had both a partial and a complete occlusion; for the control group, the registry says the correct combined participant count is 43 because that participant should not be counted twice. This note is important when interpreting the composite count as participants rather than as a sum of event categories.

The registry lists an unadjusted p-value for the secondary comparison but no reported analysis for the HIT outcome. General statistical principle: when multiple outcomes are examined, the chance of at least one apparently unusual result can increase if each is assessed without accounting for the others. The record does not report a multiplicity plan, so the secondary p-value should not be read as if a family of outcomes had been formally controlled.

Missing data can affect binary outcome comparisons if participants are not observed for the full period or if outcome status is unknown. The registry does not report the number with missing outcome status, the handling of incomplete follow-up, the analysis population, or an imputation method. General statistical principle: results can be sensitive to missingness when the probability of an observed outcome differs between groups or depends on the unobserved outcome. Without the missing-data details, the degree of that risk cannot be evaluated from the registry record.

The sample-size illustrations use the observed effect as a planning reference and state a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The illustrations show what planned group sizes would correspond to detecting stated fractions of the observed effect under those assumptions. These are planning quantities and do not describe the study’s original design process. The original sample-size justification and statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk difference is -0.004, with a 95% confidence interval from -0.030 to 0.023. The interval crosses zero, so the posted data are compatible with a lower event risk in the saline-only group, a higher event risk, or little difference. Its span indicates that the point estimate alone gives an incomplete account of the uncertainty. The estimate is not precise enough to settle the direction or size of a possible difference.

In general, a confidence interval is a range of values that reflects sampling uncertainty under the statistical method used. It does not mean there is a 95% probability that the fixed true effect lies in this particular interval. Rather, the confidence level describes the long-run coverage property of the method under its assumptions. The registry does not specify the interval-construction method, so interpretation should stay with the posted range rather than assume additional details about its calculation.

The relative measures are also imprecise. The posted risk ratio is 0.830, with an interval from 0.226 to 3.049; the odds ratio is 0.827, with an interval from 0.219 to 3.121. Both intervals include values indicating effects on either side of no relative difference. Their breadth is consistent with the limited information available from the small number of primary events.

The secondary composite risk difference is 0.082, with a 95% confidence interval from 0.003 to 0.161. This interval is on the positive side of zero, but the range still permits effects that differ considerably in size. A confidence interval can therefore support a direction of association in the observed analysis without making the effect’s magnitude precise. The outcome is also broader than the primary endpoint, so its interval addresses a different question.

Precision is distinct from statistical significance and from clinical importance. A narrow interval can estimate a small effect precisely, while a broad interval can leave uncertainty even when a point estimate appears notable. The record does not report a threshold defining a clinically important difference. Thus, these intervals describe statistical uncertainty but do not identify what magnitude would matter in practice.

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 examples based on the observed effect, not the trial’s original design calculation. For these binary participant outcomes, the figures are participants per arm; they are not total event counts. The listed assumptions are a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column describes the corresponding planning number for a 90% chance. Power is a design property under a statistical model; it is not the probability that the study’s conclusion is correct, and it is not a measure of the evidence observed after the trial.

Rows for 100%, 75%, and 50% of the observed effect ask what planning would look like if the target effect were the full observed estimate or a smaller fraction of it. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise identical assumptions. The figures can therefore rise sharply as the target effect shrinks. They are illustrations, not recommendations or evidence that the trial was designed to detect those effects.

These calculations are not observed power. They use a planning framework and assumed effect sizes; they do not describe the chance of detecting the result that actually occurred. Because the illustrations take the observed effect as their starting point, their interpretation is particularly sensitive to the uncertainty in that estimate. The confidence interval is the more direct way to assess the precision of the trial’s observed comparison.

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 = 0.023; treatment proportion p₁ = 0.019; average p̄ = 0.021.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2009 = 0.3938.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2009 = 0.1691.
4. n = (0.3938 + 0.1691)² / (-0.0038)² = 21,586.3, rounded up to 21,587 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 <- 0.0225225225225225                          # control proportion
p1 <- 0.0186915887850467                          # 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(2354118)
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 = 21,587 (80% power), 28,898 (90% power)
 75% of observed effect: n per arm = 39,250 (80% power), 52,543 (90% power)
 50% of observed effect: n per arm = 90,274 (80% power), 120,851 (90% power)
power.prop.test: 21586.3 
Simulated power at n = 21,587 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and lists secondary outcomes, but it does not report how the analysis handled multiple comparisons. There is no stated multiplicity adjustment, testing hierarchy, or procedure for controlling an overall error rate across outcomes. The posted secondary p-value is unadjusted. It should therefore be interpreted as a result for that particular comparison, not as evidence that the full set of secondary questions was evaluated under a single controlled testing plan.

Multiplicity matters because examining multiple outcomes can increase the chance that at least one result appears unusual even when no corresponding effect exists. This is a general statistical concern, not a claim that the secondary result is false. It means the secondary evidence carries less weight than a prespecified primary comparison when the analysis plan and multiplicity handling are unknown. The registry record does not say whether the outcomes were ranked or whether any analyses were exploratory.

The registry does not report missing outcome counts, reasons for missingness, methods for handling unknown status, or whether follow-up was complete for all participants. It also does not report the analysis population or whether participants were analyzed according to randomized assignment. These omissions matter because incomplete observation can affect event risks and group comparisons. The degree or direction of any resulting bias cannot be determined from the posted record.

The record does not describe interim analyses, stopping rules, or the original statistical analysis plan. It also does not state whether adjustment for other participant characteristics was planned or performed. These items are not reported in the registry record, so conclusions about them should not be inferred from the posted estimates.

The primary result can still be described as posted: the group counts, risk difference, confidence interval, and unadjusted p-value are available. But the absence of detailed analysis-population and missing-data information limits assessment of robustness. These are reporting limitations; they do not by themselves establish that the estimates are biased. They define what can and cannot be evaluated from this registry record.

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 0% reporting threshold.

The registry lists zero serious adverse events and zero other adverse events for the control group, and zero serious adverse events and zero other adverse events for the intervention group. It also lists 42 deaths in the control group and 27 in the intervention group. These figures are separate reported counts and should not be interpreted as evidence that a flushing strategy caused or prevented deaths.

The record does not provide the timing, causes, relatedness assessments, or further context needed to interpret the death counts. It also does not specify in the posted figures how adverse-event observation relates to the primary 1-year occlusion timeframe. A zero count in the adverse-event categories means no events are listed for those categories in the registry figures; it does not establish that every possible safety outcome was measured or that no other harms occurred.

These data are therefore best read as registry reporting, not as a complete comparative safety analysis. Without definitions, follow-up details, and attribution information, the counts do not support a causal safety conclusion about either flush solution.

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

The primary result shows few first complete occlusions in both groups and a small negative point estimate for the risk difference comparing saline-only flushing with heparinized-saline flushing. Its confidence interval includes zero and extends in both directions. The result therefore does not establish a clear difference in complete occlusion risk, and it does not demonstrate that the approaches are equivalent.

The secondary composite gives a different observed pattern because it includes partial as well as complete occlusion. Its unadjusted result points toward a higher risk in the saline-only group, but it is a secondary comparison and the registry does not report multiplicity control. The two endpoint results should not be collapsed into one conclusion: each concerns a distinct outcome definition, and uncertainty remains about how the wider set of outcomes should be interpreted.

In general, a randomized comparison can support inference about the assigned strategies when randomization is properly implemented and follow-up and analysis preserve the intended comparison. The registry confirms random allocation but does not provide details about allocation procedures, adherence, missing data, analysis populations, or outcome assessment. Those omissions limit how fully the design’s protections can be evaluated.

The posted data do not establish the mechanism of any occlusion, the comparative effect on all catheter complications, or the effect on outcomes beyond the registry’s stated measures and timeframe. The record lists HIT as a secondary outcome but does not give a numeric result for it. It also lists adverse-event and death counts without contextual information sufficient for causal interpretation.

Accordingly, the most defensible reading is narrow: the registry reports no clearly resolved difference for the primary complete-occlusion comparison, while the broader secondary occlusion comparison has an unadjusted signal that warrants caution. Neither finding is a general statement that one flushing approach works or does not work. The estimates describe this trial’s posted outcomes and their uncertainty, not every patient, setting, or possible outcome.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definitions matter. Complete occlusion and complete-or-partial occlusion are related but distinct outcomes. A treatment comparison can look different when the endpoint includes additional event types, so conclusions should identify exactly what was counted rather than refer broadly to “occlusion” without qualification.

It also demonstrates the difference between an estimate and its precision. The primary risk difference has a point estimate close to zero, but its interval reaches meaningful values on both sides. The point estimate alone could make the comparison appear settled; the interval makes clear that the data leave substantial uncertainty about direction and magnitude. Reporting effect estimates with confidence intervals is therefore more informative than relying only on a p-value.

Low event counts highlight another general issue. When few participants experience the primary event, estimates can be sensitive to individual outcomes and relative measures may be imprecise. This does not invalidate the result, but it argues for restraint in drawing strong conclusions from a point estimate or a single threshold-based test.

The secondary composite comparison further illustrates why unadjusted results require context. A nominally notable secondary p-value does not carry the same interpretive weight as a primary result when multiple outcomes are listed and the record does not say how multiplicity was handled. Transparent reporting of prespecified outcomes, missing data, analysis populations, and statistical plans would help readers assess how much weight to place on such findings.

Finally, planning illustrations based on an observed effect are not evidence of the trial’s design adequacy. They are sensitive to the uncertain effect estimate and should be read as hypothetical planning scenarios. Distinguishing those calculations from observed results and original design assumptions is essential for sound statistical interpretation.

18. Limitations

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

The registry record gives limited detail for evaluating who entered the study and how the comparison was carried out. It reports randomized allocation and no masking, but does not describe eligibility criteria, randomization procedures, allocation concealment, adherence, or outcome assessment. These details would help readers judge whether the observed groups and measurements support the intended comparison.

The intervention description is also incomplete for understanding treatment exposure. The control flush is described as 20mL saline + 5mL heparin 100 units/mL; q 3 months, while the saline-only arm description does not state a volume or interval. The registry record does not report whether the same schedule was used in both groups or how deviations were handled.

The primary outcome record includes a note that one participant had both a partial and a complete occlusion, and that the correct control-group count for participants with either type is 43 rather than counting the person twice. This clarifies the control composite count, but the record does not provide participant-level event information or explain whether similar overlap occurred in the other group.

Missing outcome status, follow-up completeness, and analysis populations are not reported in the registry record. Nor does it report the statistical test, analysis plan, multiplicity handling, interim analyses, or original sample-size justification. These omissions prevent a fuller assessment of robustness and design assumptions.

Finally, the numerical HIT result is not posted, and the adverse-event figures lack contextual details about timing and relatedness. These are reporting limitations rather than proof of a problem with study conduct. They constrain the scope of conclusions that can be drawn from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Maintaining Patency in Implanted Port Catheters — NCT02354118.
• Registry record last updated 2022-10-12; status last verified 2022-09.
• Results first posted 2022-09-14.
• 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 record describes NCT02354118, “Maintaining Patency in Implanted Port Catheters,” sponsored by TriHealth Inc. It lists a completed, randomized, parallel-group trial with no masking and an enrollment of 436. The comparison was saline-only catheter flushing versus heparinized-saline flushing.

The primary outcome was the number of participants with a first complete occlusion within 1 year. The posted comparison estimates a risk difference of -0.004, with a 95% confidence interval from -0.030 to 0.023 and an unadjusted p-value of 0.779. The interval includes zero and does not resolve the direction of a possible difference.

A secondary complete-or-partial occlusion outcome has a different observed pattern, but it is unadjusted and should be interpreted cautiously. A numeric result for the listed HIT outcome is not reported in the registry record. Details of missing data, analysis populations, multiplicity procedures, and the original design assumptions are also not reported.