Effectiveness of the Rapid Intravascular Start (RIVS) System Versus Conventional Catheter: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effectiveness of the Rapid Intravascular Start (RIVS) System Versus Conventional Catheter (NCT00914069), a randomized na study. The primary outcome is IV Insertion Success Rate at First Attempt IV Insertion Success Rate at First Attempt.

2. Clinical Question

The registry asks whether the Rapid Intravascular Start (RIVS) system can achieve more successful first-attempt peripheral intravenous (PIV) insertions than a conventional catheter, while avoiding an increase in complications and procedure time. The primary outcome is a participant-level count of successful insertions at the first attempt. The posted results give 60 successes among 84 participants in the RIVS group and 51 among 88 in the conventional-access group.

The official title frames the intended population as children, oncology patients, and elderly patients. The registry's population field for the primary outcome is blank, however, and it does not report eligibility criteria or the distribution of participants across those groups. It is therefore not possible to tell from the record which of those groups contributed participants, or how well the findings represent any one group.

The comparison is between two vascular-access devices: RIVS and conventional vascular access. The central question is about first-attempt insertion success; procedure time, second-stick success, and minor complications are also listed as secondary outcomes. The trial's brief summary describes the comparison as a test of a higher first-attempt success rate without a significant increase in complications or procedure time. That statement describes the study's hypothesis, not a conclusion established by the hypothesis itself.

3. Trial Design

The record describes a randomized, parallel-group controlled trial with no masking. Participants were assigned to RIVS vascular access or conventional vascular access. Because masking is listed as none, the record does not describe a blinded comparison. Details about who generated the allocation sequence, how assignment was concealed, or who assessed the outcome are not reported in the registry record.

The listed enrollment is 175. For the posted primary outcome, the group denominators are 84 for RIVS and 88 for conventional access. The registry does not provide a participant-flow account that reconciles enrollment with these outcome denominators, so the reason for any difference cannot be determined from the record. It also does not describe the analysis population, such as whether results followed initial randomized assignment or included only participants with an evaluable outcome.

The primary completion date is 2013-07, and the study status is terminated. The start date is 2009-06. The reason for termination and whether the study ended according to its original schedule are not reported in the registry record. The record does not state whether there were interim analyses or changes to the protocol.

The trial lists five outcome measures and two analyses, while three secondary outcomes are posted: time required to obtain access, second-stick success rate, and a summary of minor complications. The registry record does not describe the full statistical analysis plan, how the outcomes were prioritized beyond the listed primary outcome, or how many participants were intended for each arm. The sample-size illustrations associated with the posted results are based on observed effects and should not be mistaken for the trial's original design plan.

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: Prior to assignment to groups, two subjects withdrew from the study. Also prior to group assignment, one subject did not have a consent form and was excluded from the study.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as IV Insertion Success Rate at First Attempt IV Insertion Success Rate at First Attempt, measured over An access attempt usually ranges from 0 to 45 minutes in duration..

The primary endpoint is the number of participants with successful IV insertion at the first attempt. The registry defines success as a sequence of procedural steps: initial vein penetration evidenced by blood flashback, guidewire deployment, catheter advancement into the vein, withdrawal of the needle and guidewire, and flushing of the IV. A secured, flushed IV is described as indicating successful PIV placement. An access attempt usually ranges from 0 to 45 minutes in duration.

This endpoint captures whether the initial attempt results in a usable access, rather than merely whether the vein was entered. That distinction makes it a clinically interpretable measure of the immediate insertion process. The endpoint is binary at the participant level: each participant contributes either a success or not a success for the first attempt. It does not, on its own, describe later access attempts, time to access, or complications after placement; those issues are addressed separately among the listed secondary measures.

The primary outcome is reported as counts of participants with success and group denominators. The registry does not report a separate definition for how participants with incomplete procedure records, protocol deviations, or missing outcome assessments were treated. Nor does it state whether the person judging each procedural step was independent of the intervention team. Those details matter when interpreting a first-attempt outcome, especially in an unmasked device comparison.

7. Results Posted in the Registry

• Conventional Vascular Access: 58.0% (51/88) versus 71.4% (60/84) on control; risk difference -13.5 percentage points (95% CI -27.6 to 0.7), risk ratio 0.81 (0.65–1.01); unadjusted two-proportion z-test p = 0.065.

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.

Time Required to Obtain Access

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Conventional Vascular Access: mean 5.00 versus 4.00 on control; difference 1.00 (95% CI -0.35 to 2.35), standardized effect d = 0.22; z-test p = 0.147.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conventional Vascular Access and the control. The interval gives the range of effects that remain compatible with the data.

Second Stick Success Rate

• 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:
  • Conventional Vascular Access: 50.0% (18/36) versus 43.5% (10/23) on control; risk difference 6.5 percentage points (95% CI -19.5 to 32.5), risk ratio 1.15 (0.65–2.03); unadjusted two-proportion z-test p = 0.625.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conventional Vascular Access and the control. The interval gives the range of effects that remain compatible with the data.

Summary of Minor Complications

• 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:
  • Conventional Vascular Access: 0.0% (0/88) versus 1.2% (1/84) on control; risk difference -1.2 percentage points (95% CI -3.5 to 1.1); unadjusted two-proportion z-test p = 0.305.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Conventional Vascular Access and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints extend the primary question beyond first-attempt insertion: they address procedure time, success at a second stick, and minor complications. Across these measures, the directions do not consistently favor one access approach. The point estimate for procedure time favors shorter time with RIVS, the second-stick success estimate points in the other direction, and the minor-complication record contains an isolated event in the RIVS group. These outcomes therefore do not form a uniform secondary pattern that independently confirms the primary result.

The relationship to the primary endpoint should be interpreted with care. A first-attempt success outcome concerns the initial insertion attempt, while second-stick success concerns a later attempt and procedure time captures duration. A minor-complication summary addresses a different aspect of the procedure and subsequent access. The endpoints are related in a broad procedural sense, but one should not assume that the same participants contributed to every endpoint or that one outcome mechanically explains another. The registry does not report the analysis populations or participant-level connections among these outcomes.

Unadjusted secondary results carry less weight when several outcomes are examined because multiple comparisons create more opportunities for apparently notable results to arise by chance. In general, multiplicity procedures can control how error rates are interpreted across a family of tests. The registry does not report a multiplicity adjustment, a hierarchy among secondary hypotheses, or a plan for interpreting these results jointly. Consequently, secondary p-values and point estimates should be treated as descriptive evidence rather than as conclusive standalone tests. Their uncertainty and the limited analysis detail further constrain interpretation.

The registry lists five outcome measures, but only three secondary outcomes are posted in the information summarized for the trial. The status of the other measures and the reason only these secondary results appear are not reported in the registry record. This incomplete context is another reason not to assign decisive weight to a pattern among the posted secondary endpoints.

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

• Time Required to Obtain Access
• Second Stick Success Rate
• Summary of Minor Complications

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either had a successful first-attempt insertion according to the registry definition or did not. The group results are presented as event counts and denominators. A risk difference compares the two groups' event proportions by subtraction. In the recalculation, the contrast is conventional access minus RIVS; a negative value therefore points toward fewer first-attempt successes in the conventional group. This direction is a description of the estimate, not a declaration that one device is superior.

What does the confidence interval describe?

In general, a confidence interval gives a range of effect estimates that are reasonably compatible with the observed data under the assumptions of the method used. It reflects sampling uncertainty, not the range of individual outcomes and not the probability that a particular treatment effect is true. For the primary risk difference, the interval crosses zero. Zero corresponds to no difference in the risk-difference scale, so the interval includes both no difference and effects in either direction. The width also signals that the estimate is not very precise.

What does a p-value add?

In general, a p-value measures how unusual data at least as extreme as those observed would be under a specified null hypothesis and analysis method. It is not the probability that the null hypothesis is true, nor a direct measure of the size or practical importance of an effect. The recalculated unadjusted p-value is 0.065, while the registry's reported Fisher Exact result is p = 0.05. Because these values are associated with different descriptions of the analysis, and the record does not give further calculation details, they should not be treated as interchangeable or used to infer a missing analysis plan.

Why use Fisher Exact for a binary outcome?

In general, Fisher's exact test evaluates an association in a two-by-two table and calculates a p-value using the table margins. It is one method for comparing a binary outcome across groups. The registry identifies Fisher Exact as the method for the reported primary analysis. It does not give a confidence interval for that analysis or additional details such as the exact test specification. A test result and an effect estimate answer related but different questions: the test evaluates data under a null hypothesis, while the risk difference describes the magnitude and direction of the observed contrast.

How should the secondary measures be read?

Procedure time is a continuous measure, reported as a mean with a standard deviation. In general, a mean summarizes the center of measured values, while a standard deviation describes their spread. The posted group means are 4.0 minutes for RIVS and 5.0 minutes for conventional access, with standard deviations of 4.0 and 5.0 minutes, respectively. The recalculated mean difference is 1.0 minute for conventional access minus RIVS; its confidence interval includes zero. The record does not report a sponsor analysis for this endpoint.

Second-stick success and minor complications are also binary outcomes. Their counts and denominators permit unadjusted group comparisons, but the estimates are based on the participants represented in those outcome records. The registry does not explain why the denominators for second-stick success differ from the primary outcome denominators or how participants became eligible for that measure. This makes it important not to treat the secondary results as though they necessarily arose from the same analysis population as the primary endpoint.

Why do over-dispersion and model choice matter?

General explanation: for count or continuous outcomes, a statistical model can make assumptions about how variable observations are. Over-dispersion means the observed variability is greater than a model expects; if it is ignored, standard errors may be too small and confidence intervals too narrow. The posted primary endpoint is binary and the posted time endpoint is summarized with means and standard deviations. The registry does not report a model-based adjustment for over-dispersion, and no such adjustment should be inferred from these summaries.

The record does not report covariate adjustment, stratification, a prespecified analysis population, handling of missing observations, or correction for multiple comparisons. These omissions limit how fully the analyses can be reproduced or assessed. In particular, a randomized assignment does not by itself establish how participants with missing outcomes were handled, or whether all randomized participants were included in the reported comparison. The posted summaries are therefore best understood as the results recorded for the listed groups and outcomes, with the analysis details left incomplete.

11. Confidence Intervals and Precision

Precision is about how tightly the data constrain an effect estimate. The primary risk-difference confidence interval extends from -0.276 to 0.007. It crosses zero, meaning the data are compatible with no difference as well as with effects favoring either arm. The interval is broad enough that the estimate does not pin down a single likely magnitude. The observed direction favors RIVS, but the uncertainty should be considered alongside that direction rather than treated as an afterthought.

A confidence interval does not establish that every value inside it is equally plausible, and it does not cover every uncertainty in a trial. It reflects sampling uncertainty under the interval's statistical assumptions. It does not account for possible bias from unmasked outcome assessment, unreported missing-data handling, or uncertainty about which participants were included. The registry does not provide a confidence interval for its Fisher Exact analysis.

For procedure time, the recalculated mean difference is 1.0 minute, and its confidence interval runs from -0.350 to 2.35. This interval also includes no difference and permits effects in either direction. The secondary binary outcomes have wide intervals as well, reflecting limited precision in those comparisons. These intervals are not evidence that the groups are equivalent; demonstrating equivalence would require a defined equivalence margin and an analysis designed for that question, neither of which is reported in the registry record.

Precision also depends on what the study was designed to detect. The record does not report the trial's original sample-size assumptions or target effect. The planning illustrations based on observed effects are not a substitute for that missing design information. In addition, the termination status and absent participant-flow details make it difficult to judge whether the posted group denominators represent the intended analysis population.

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 translate the observed effects into planning examples. For the binary outcomes and the continuous procedure-time outcome, figures are participants per arm, not total events. The record's assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the chosen effect under the planning assumptions, if that effect is real and the assumed analysis applies. The 90% power column uses a higher chance of detection and consequently requires more participants per arm for the same effect. These are planning calculations, not a statement about the probability that the observed trial result is correct.

The rows illustrate planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning calculation calls for more participants. For example, the primary endpoint illustration lists 197 participants per arm for 80% power when planning for 100% of the observed effect, and 751 per arm when planning for 50% of that effect. The corresponding 90% power figures are 263 and 1,005 participants per arm. The time-to-event convention of reporting total events does not apply to these listed outcomes.

These figures are not observed power. They are hypothetical planning illustrations derived from the observed effects, and they do not reveal what assumptions were used when the trial was designed. The curve should be interpreted in the same planning context: it depicts how the illustrated participant requirement changes with the effect fraction, not the trial's actual recruitment history or the likelihood that a result is true.

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 = 0.714; treatment proportion p₁ = 0.580; average p̄ = 0.647.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6759 = 1.3247.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6691 = 0.5632.
4. n = (1.3247 + 0.5632)² / (-0.1347)² = 196.3, rounded up to 197 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 <- 0.714285714285714                          # control proportion
p1 <- 0.579545454545455                          # 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(914069)
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 = 197 (80% power), 263 (90% power)
 75% of observed effect: n per arm = 342 (80% power), 458 (90% power)
 50% of observed effect: n per arm = 751 (80% power), 1,005 (90% power)
power.prop.test: 196.3 
Simulated power at n = 197 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. Analyses Reported by the Sponsor

The registry reports a Fisher Exact analysis for the primary outcome, with p = 0.05. A separate unadjusted recalculation from the posted group summaries gives p = 0.065. The registry also gives 60 successful first attempts among 84 participants in the RIVS group and 51 among 88 in the conventional group. The recalculation expresses the difference as conventional access minus RIVS and reports a confidence interval that crosses zero.

The two p-values should not be treated as if they were the same calculation with identical specifications. The registry does not report enough detail to reconcile the difference, including the test specification beyond naming Fisher Exact for its own analysis. The discrepancy flag is not raised for this comparison, but that does not make the analyses identical. The recalculation is a simple, unadjusted assessment of the posted summary statistics; it does not replace the trial's own analysis or account for unreported design and analysis details.

The sponsor analysis supplies a p-value but no effect estimate or confidence interval in the posted analysis entry. The recalculated estimate adds a magnitude and uncertainty interval, but it is not adjusted for covariates or other possible analysis choices. Read together, the entries show the sponsor's stated test result and a separate descriptive estimate, while leaving the precise relation between the calculations unresolved in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when multiple outcomes, comparisons, or analyses are examined. In general, the more statistical tests considered, the more opportunities there are for a result to appear noteworthy by chance, even when no underlying effect exists. The registry lists five outcome measures and two analyses, and three secondary outcomes are posted. It does not report whether the primary and secondary outcomes formed a prespecified family for statistical testing, whether one outcome was prioritized in a testing sequence, or whether p-values were adjusted for multiple comparisons.

The record identifies a primary outcome, which helps distinguish the central trial question from the secondary measures. However, it does not provide the full statistical analysis plan or clarify how the two listed analyses relate to all outcomes. It is therefore not possible to determine whether the reported p-values were selected from a larger set of analyses or whether the analysis sequence was prespecified. The unadjusted secondary results should be interpreted with that uncertainty in mind.

Missing-data handling is also not reported in the registry record. There is no description of how missing primary or secondary outcome information was handled, whether imputation was used, or what assumptions informed any such approach. The record does not explain the difference between the enrollment figure and the denominators reported for the outcomes, and it does not provide a participant-flow account. That gap should not be interpreted as proof that participants were lost or excluded for any particular reason.

The analysis populations are not described. In particular, the registry does not say whether the primary analysis included all randomized participants, only participants with observed outcomes, or another defined group. It also does not report whether the analysis followed randomized assignment in the presence of deviations from assigned treatment. These details are necessary to assess how the randomized comparison was preserved in the analysis.

Interim analyses, stopping rules, and changes to the statistical plan are not reported in the registry record. The study is listed as terminated, but the reason for termination and its relationship, if any, to the planned analyses are not stated. These unknowns limit a complete assessment of multiplicity, missingness, and the analysis populations.

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 non-serious adverse event terms

The serious-adverse-event figures list 0 events among 84 participants at risk in the RIVS group and 0 among 88 at risk in the conventional group. The registry lists no serious-event terms. These counts describe the serious events recorded for the groups; they do not establish that all possible serious harms have been ruled out. With no serious events recorded in either group, the data provide limited information about differences in uncommon harms.

The adverse-event record also lists one other adverse event in the RIVS group and none in the conventional group. The registry does not supply further detail about that event in the posted information. The death fields do not contain a count, so deaths are not reported in the registry record; a blank field should not be read as a confirmed zero. The registry's minor-complication outcome is a separate measure from the serious-adverse-event listing and should not be treated as a complete account of every safety outcome.

The record identifies the period for minor complications as after PIV placement until catheter removal, usually within 4 days. It does not report the follow-up period for serious adverse events or detailed methods for collecting adverse events. Safety interpretation is therefore limited to the figures and timeframes explicitly recorded.

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

The results show a higher observed count of first-attempt successes in the RIVS group than in the conventional-access group. The unadjusted risk-difference estimate is in the direction favoring RIVS, but its confidence interval includes no difference and allows effects in either direction. The posted data therefore do not define the size of any true difference precisely. Neither the event counts nor the p-values alone establish that one approach is superior.

The sponsor's reported Fisher Exact p-value and the separate unadjusted recalculation are different summaries, and the registry does not explain the difference. The primary finding should be read with both the effect estimate and its uncertainty in mind. A p-value does not indicate how important a difference would be in practice, and it does not measure the probability that the observed direction will hold in another study.

The secondary outcomes add information about time, later attempts, and minor complications, but their directions are mixed and their analyses are unadjusted. The registry does not report whether multiplicity was addressed or how the secondary analysis populations were defined. The absence of recorded serious adverse events in either arm is reassuring only as a description of the posted counts; it cannot rule out harms that were not captured or too uncommon to appear in the recorded participants.

The trial title names children, oncology patients, and elderly patients, but the record does not provide subgroup-specific results or enough eligibility information to establish how each group was represented. It is not possible to infer that the overall comparison applies equally to those populations. The terminated status, lack of a reason for termination, and missing information on participant flow and analysis populations add further limits.

In short, the registry records an observed difference in first-attempt counts but leaves substantial uncertainty about its magnitude and the wider interpretation. The results do not establish comparative effectiveness for every population named in the title, do not demonstrate equivalence, and do not settle safety questions beyond the adverse-event information recorded.

18. Why This Trial Matters Statistically

This trial illustrates why a comparison of event counts should be paired with an effect estimate and an uncertainty interval. The observed counts alone suggest a direction, but they do not show how much uncertainty surrounds the comparison. The risk-difference interval crosses zero and spans a meaningful range in both directions, so the point estimate cannot be treated as a precise answer to the trial question.

It also illustrates the distinction between a trial's reported analysis and a recalculation from posted summaries. The registry names Fisher Exact for its analysis, while an unadjusted recalculation yields a different p-value and supplies an effect estimate with an interval. These pieces of information are complementary but not interchangeable. Without a fuller statistical plan, differences between methods cannot be fully investigated.

The secondary measures demonstrate why a coherent interpretation matters more than selecting a single favorable result. Procedure time, second-stick success, and minor complications do not point uniformly in one direction. When multiple endpoints are considered without a reported multiplicity strategy, isolated findings deserve restraint, especially when their analysis populations and missing-data handling are unclear.

Finally, the record makes clear that a randomized design does not resolve every interpretive question by itself. Masking, participant flow, outcome assessment, analysis populations, and termination context all affect how confidently posted results can be understood. Reporting those details allows readers to assess not only the numerical estimates but also how the estimates were produced and to whom they may apply.

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.

Several limitations are specific to the available record. The study is listed as terminated, but the reason for termination is not reported. It is not clear whether the termination followed the original plan, and the record does not state whether any interim looks at the data occurred. No conclusion about early stopping or its effect on the results can be drawn from the status alone.

The official title identifies children, oncology patients, and elderly patients, yet eligibility criteria, participant characteristics, and results for these groups are not reported. This prevents assessment of representation and of whether the overall result might differ across those populations. The primary outcome population field is blank.

The trial was unmasked. The registry does not describe who assessed first-attempt success, whether assessments were standardized across staff, or whether outcome assessment was independent. Those details could matter for a procedural endpoint involving several judgments about whether insertion steps were completed successfully.

The record does not explain why the primary outcome denominators differ from the listed enrollment or why the second-stick outcome has different group denominators. No participant flow, missing-data method, or analysis-population definition is posted. This makes it difficult to assess completeness or determine how closely the analysis reflects randomized assignment.

Finally, the posted record lacks the trial's original sample-size assumptions and a full statistical analysis plan. It does not report multiplicity handling, covariate adjustment, or detailed safety surveillance methods. The observed-effect planning examples cannot fill those gaps, and the adverse-event counts should not be taken as an exhaustive safety account.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effectiveness of the Rapid Intravascular Start (RIVS) System Versus Conventional Catheter — NCT00914069.
• Registry record last updated 2017-04-13; status last verified 2017-03.
• Results first posted 2017-04-13.
• 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.

23. Record Summary

NCT00914069 is a randomized, unmasked, parallel-group trial comparing RIVS vascular access with conventional vascular access for PIV insertion. The listed enrollment is 175, the primary completion date is 2013-07, and the study status is terminated. The official title names children, oncology patients, and elderly patients.

The primary endpoint is successful IV insertion at the first attempt. The registry posts 60 successes among 84 RIVS participants and 51 among 88 conventional-access participants. The sponsor's reported primary analysis is Fisher Exact, with p = 0.05; a separate unadjusted recalculation gives p = 0.065 and an interval that crosses no difference.

Three secondary outcomes are posted, but the record does not report a full statistical plan, participant-flow details, missing-data handling, or analysis-population definitions. The reason for termination is not reported in the registry record. Interpretation should remain centered on the observed results and their uncertainty, with these reporting limitations in view.