Comparison of Three Techniques for Ultrasound-guided Internal Jugular Cannulation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Three Techniques for Ultrasound-guided Internal Jugular Cannulation (NCT01966354), a randomized na study. The primary outcome is Cannulation Success.

2. Clinical Question

The trial’s stated purpose was to assess the efficacy and safety of three ultrasound assistance techniques in terms of cannulation success and prevention of complications. The posted primary results compare each alternative technique with the long-axis, in-plane approach; they do not provide a direct statistical comparison between the two alternative approaches. The secondary outcomes cover number of attempts, first-attempt cannulation, cannulation time, mechanical complications, and infectious complications. Numeric results are posted for the first three of these, while results for mechanical and infectious complications are not reported in the registry record.

The clinical question is therefore about comparative procedural outcomes under the three specified imaging and needle orientations. It is not a comparison with cannulation without ultrasound, and the registry record does not describe other possible approaches or settings. The available results address the recorded outcomes and their uncertainty; they do not by themselves establish how the techniques perform in populations or circumstances not described in the record.

3. Trial Design

The registry record describes a randomized, single-masked, parallel-group trial. Enrollment is listed as 220, and the study status is completed. The phase is listed as NA. The start is recorded as 2012-03 and primary completion as 2013-03. The listed intervention is an ultrasound-guided internal jugular venous approach, with participants assigned to one of three specified ultrasound and needle orientations.

The three arms were long-axis, in-plane needle; short-axis, out-of-plane needle; and oblique-axis, in-plane needle. The arm descriptions explain the orientation of the vein image and needle relative to the ultrasound plane. The registry does not report further details about the randomization sequence, concealment, or how masking was implemented. It also does not report the original sample-size justification or the trial’s planned statistical analysis.

The posted primary outcome is cannulation success, recorded at the end of the cannulation process, with a maximum timeframe of 180 seconds. The posted arm results are 73 participants with success among 75 in the long-axis arm, 71 among 73 in the short-axis arm, and 68 among 72 in the oblique-axis arm. The comparison estimates are against the long-axis arm. The record contains no reported analysis entries, so the comparison statistics on the page should be read as unadjusted recalculations from the posted arm summaries rather than as a documented sponsor analysis.

The registry also lists five secondary outcomes. Numeric results are present for number of cannulation attempts, first-attempt cannulation, and cannulation time. Results for mechanical complications and infectious complications are not reported in the registry record. This distinction matters: an outcome may be listed as planned or relevant without a corresponding result being posted. The registry record does not describe a prespecified hierarchy or adjustment plan for interpreting multiple 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

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 Cannulation Success, measured over At the end of the cannulation process (180 seconds, maximum).

The primary endpoint is cannulation success, recorded as the number of participants meeting the registry’s success definition. A procedure counted as successful if a flexible guidewire was inserted into the internal jugular vein during the first 180 seconds after the Seldinger needle pierced the skin. If guidewire insertion took longer than 180 seconds, or the guidewire could not be inserted into the selected vein, the procedure counted as unsuccessful. The outcome was recorded at the end of the cannulation process.

This endpoint captures whether the intended guidewire placement was achieved within the specified time limit. It is a binary outcome: each recorded procedure is classified as successful or unsuccessful under the stated rule. The endpoint therefore combines the occurrence of guidewire insertion with a time boundary. It does not, on its own, describe the number of needle passes, the time taken among successful procedures, or the nature of any complication. Those are distinct outcomes, some of which appear among the trial’s secondary measures.

The endpoint is relevant to the trial’s stated objective because the study set out to compare cannulation success across the techniques. However, the registry record does not report a threshold for what difference would be clinically important, nor does it give further detail about handling cases where outcome assessment was incomplete. The primary results should accordingly be read as comparisons of the recorded success classifications, with the posted uncertainty, rather than as a complete account of every aspect of procedural performance.

7. Results Posted in the Registry

• Short Axis, Out-of-plane Needle: 97.3% (71/73) versus 97.3% (73/75) on control; risk difference -0.1 percentage points (95% CI -5.3 to 5.2), risk ratio 1.00 (0.95–1.05); unadjusted two-proportion z-test p = 0.978.
• Oblique Axis, In-plane Needle: 94.4% (68/72) versus 97.3% (73/75) on control; risk difference -2.9 percentage points (95% CI -9.3 to 3.5), risk ratio 0.97 (0.91–1.04); unadjusted two-proportion z-test p = 0.376.

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 Cannulation Attempts

• 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:
  • Short Axis, Out-of-plane Needle: mean 1.51 versus 1.92 on control; difference -0.41 (95% CI -0.79 to -0.03), standardized effect d = -0.35; z-test p = 0.034.
  • Oblique Axis, In-plane Needle: mean 1.37 versus 1.92 on control; difference -0.55 (95% CI -0.91 to -0.19), standardized effect d = -0.48; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Short Axis, Out-of-plane Needle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Oblique Axis, In-plane Needle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

First Attempt Cannulation

• 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:
  • Short Axis, Out-of-plane Needle: 69.9% (51/73) versus 52.0% (39/75) on control; risk difference 17.9 percentage points (95% CI 2.4 to 33.3), risk ratio 1.34 (1.03–1.75); unadjusted two-proportion z-test p = 0.026.
  • Oblique Axis, In-plane Needle: 73.6% (53/72) versus 52.0% (39/75) on control; risk difference 21.6 percentage points (95% CI 6.4 to 36.8), risk ratio 1.42 (1.09–1.83); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Short Axis, Out-of-plane Needle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Oblique Axis, In-plane Needle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Cannulation Time

• 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:
  • Short Axis, Out-of-plane Needle: mean 35.00 versus 46.10 on control; difference -11.10 (95% CI -20.91 to -1.29), standardized effect d = -0.36; z-test p = 0.027.
  • Oblique Axis, In-plane Needle: mean 41.20 versus 46.10 on control; difference -4.90 (95% CI -14.80 to 5.00), standardized effect d = -0.16; z-test p = 0.332.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Short Axis, Out-of-plane Needle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oblique Axis, In-plane Needle and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide several views of procedural performance: number of cannulation attempts, success at the first attempt, and elapsed cannulation time. Their overall pattern is not a single uniform signal across all measures. The two alternative approaches show lower average attempt counts than the long-axis approach in the posted summaries, while the first-attempt counts are higher. The time comparisons differ in their estimates and uncertainty. These outcomes describe related but distinct aspects of the procedure, and should not be treated as interchangeable measures of the primary endpoint.

The primary endpoint asks whether guidewire placement occurred within the stated time limit. A participant can meet that definition without necessarily succeeding on the first attempt, and the number of attempts and total time describe additional features. The secondary outcomes can therefore complement the primary endpoint by showing aspects of process, but they do not revise the primary success classification or establish a broader measure of benefit.

The registry lists mechanical complications and infectious complications as secondary outcomes, but their numeric results are not reported in the registry record. Adverse-event counts appear separately; they should not be substituted for missing results on those named secondary outcomes because the record does not establish that their definitions or ascertainment are the same.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for chance findings, and the registry does not report a multiplicity strategy or analysis hierarchy. The absence of reported analyses also leaves unclear which comparisons were prespecified and how the sponsor intended to interpret them. Secondary findings are best treated as descriptive and hypothesis-generating unless supported by a documented analysis plan and appropriate confirmation. Their agreement or disagreement with the primary endpoint can inform interpretation, but should not be used to select only the most favorable outcome.

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

• Number of Cannulation Attempts
• First Attempt Cannulation
• Cannulation Time
• Mechanical Complications
• Infectious Complications

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint such as cannulation success, a risk difference expresses the difference between the proportion with the event in one arm and the proportion in the reference arm. A value below zero means the event proportion in the compared arm is lower in the observed data; a value above zero means it is higher. This is a difference in proportions, not a ratio. The primary comparison estimates are risk differences, so their scale directly describes the absolute contrast in observed success proportions.

A confidence interval describes a range of values reasonably compatible with the data and the statistical model used to construct it. It conveys precision as well as direction. If an interval includes zero for a risk difference, the data are compatible with no difference under that calculation, as well as with values on either side of zero. This does not establish that the true difference is exactly zero. A p-value addresses compatibility with a specified null model; it is not the probability that the null hypothesis is true, and it does not measure clinical importance.

The posted primary comparisons are unadjusted recalculations based on the arm summaries. The registry record has no reported analysis entries and does not describe the sponsor’s analysis methods. Thus, the posted p-values and intervals should not be mistaken for an analysis plan or for results that the record attributes to a particular prespecified model. The same caution applies to the recalculated secondary comparisons.

For continuous outcomes, the registry reports arm means and standard deviations. A mean difference compares the average outcome in a non-reference arm with the average in the long-axis, in-plane arm. Its interpretation depends on the units: the attempts outcome is measured in attempts and cannulation time is measured in seconds. The standard deviation describes variability among observations within an arm; it is not the uncertainty around the mean difference. The confidence interval around a mean difference expresses uncertainty in the estimated contrast.

Binary and continuous measures answer different questions. Success and first-attempt cannulation are recorded as counts of participants with the event. Attempts and time are summarized as means and standard deviations. A comparison in mean attempts does not directly state how many participants succeeded, and a mean time does not by itself explain how time was distributed or how unsuccessful procedures contributed. The endpoint definitions and summaries should therefore be kept distinct rather than blended into one overall measure of performance.

Why do unadjusted comparisons need care?

When many outcomes or group comparisons are examined, the chance of seeing an apparently unusual result by chance can increase. Multiplicity methods can control or otherwise address this issue, but the registry record does not report a planned adjustment strategy, a hierarchy of outcomes, or whether any interim analyses were conducted. Those details are not reported in the registry record. The unadjusted p-values consequently provide less protection against chance findings across a set of analyses than a documented, prespecified multiplicity strategy would.

This concern is especially relevant to secondary outcomes, which can be useful for describing how the techniques differ but are often less decisive when there are multiple measures and no reported adjustment plan. A p-value below a conventional threshold does not, by itself, establish that a finding was prespecified or robust to multiplicity. Conversely, a p-value above a threshold does not establish the absence of a difference. Estimates and confidence intervals, interpreted alongside study design and the prespecified analysis if available, are more informative than a threshold alone.

What does the planning illustration represent?

The sample-size planning illustration uses the observed effect as its starting point and applies the stated fractions of that effect. It is a forward-looking planning calculation under its listed assumptions, not an account of the trial’s original design justification. Its results depend on assumptions including the effect chosen for planning, significance level, allocation, and approximation method. The registry record does not report whether those assumptions match the trial’s original design choices.

Planning calculations are sensitive to the effect used. If a future study aims to detect a smaller difference than the observed one, it generally needs more participants under otherwise comparable assumptions. The table’s figures should therefore be read as illustrations conditional on the stated inputs, not as guarantees about a future study. They do not supply information about whether the original trial was designed to detect a particular effect or whether its original target was met.

In general, over-dispersion occurs when outcome variability is greater than assumed by a model; if ignored, uncertainty can be understated. That concept is relevant when choosing models for outcomes with extra variability, but the registry record does not report an over-dispersion assessment or a model that would permit one to be evaluated. For the posted continuous outcomes, the available summaries are means and standard deviations. The record does not provide distributions or model diagnostics.

11. Confidence Intervals and Precision

The primary risk-difference interval for short-axis, out-of-plane cannulation is -0.053 to 0.051, around an estimate of -0.001. The interval crosses zero and extends in both directions. It therefore does not isolate one direction of difference, and it leaves uncertainty about the size of any advantage or disadvantage. The primary interval for oblique-axis, in-plane cannulation is -0.093 to 0.035, around an estimate of -0.029. It also crosses zero and includes values on either side.

Confidence intervals are useful because they show more than whether an unadjusted p-value crosses a threshold. Here, they show that the estimates are imprecise enough to remain compatible with a range of comparative outcomes. The registry record does not give a clinically important difference threshold, so it is not possible to say whether every value in either interval would be practically negligible or important. Nor should an interval crossing zero be interpreted as proof of equivalence.

The sample sizes in the arms are 75, 73, and 72, and the observed success counts are close to the arm denominators. With binary outcomes, the information available for estimating a difference depends on the observed event pattern as well as the number of observations. The posted intervals reflect uncertainty in the risk-difference calculations, but the registry record does not report an original precision target or a design justification against which to judge them.

The intervals for the secondary outcomes also vary in width and in whether they include a null difference. Those results should be considered in their own units and alongside the multiplicity and reporting limitations. More precision would narrow uncertainty, but it would not by itself address whether outcomes were prespecified, whether the analysis was appropriate, or whether the difference matters clinically.

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, not observed trial results. For these comparisons, the figures are participants per arm. 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 the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size assumptions or justification.

The 80% power column gives the number of participants per arm that the stated planning calculation estimates would be needed to have an 80% chance of detecting the chosen effect under the listed assumptions, if that effect and model assumptions applied. The 90% power column describes the corresponding planning target for a 90% chance. These are prospective operating characteristics of a hypothetical design, not probabilities that the observed trial result is correct.

The rows that use smaller fractions of the observed effect represent more modest differences to detect. Smaller effects generally require more participants to distinguish them from random variation under otherwise similar assumptions. The figures can therefore rise substantially as the effect used for planning becomes smaller. The sample-size curve expresses the same general relationship visually; it should be read as conditional on the planning assumptions, not as an empirical result from the trial.

Because these calculations use the observed effect as a reference, they should not be treated as an independent estimate of the effect that a future study ought to expect. Observed effects can be uncertain, especially in a trial with limited precision. The illustration is not observed power: observed power is not a substitute for interpreting the estimated effects and confidence intervals. The useful reading is how planning requirements change under the stated assumptions and effect choices, not whether the completed trial had a particular probability of success.

The registry notes that time-to-event planning tables, when present, give total events, but these posted comparisons are not time-to-event outcomes. The listed figures for the comparisons are participants per arm, not total events or a combined total across arms.

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 = 0.973; treatment proportion p₁ = 0.973; average p̄ = 0.973.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2294 = 0.4495.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2294 = 0.1930.
4. n = (0.4495 + 0.1930)² / (-0.0007)² = 773,502.0, rounded up to 773,502 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 <- 0.973333333333333                          # control proportion
p1 <- 0.972602739726027                          # 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(1966354)
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 = 773,502 (80% power), 1,035,500 (90% power)
 75% of observed effect: n per arm = 1,370,599 (80% power), 1,834,843 (90% power)
 50% of observed effect: n per arm = 3,073,683 (80% power), 4,114,789 (90% power)
power.prop.test: 773502 
Simulated power at n = 773,502 per arm: 0.802 (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 trial has a primary outcome and multiple secondary outcomes, with comparisons of each alternative technique against the long-axis, in-plane approach. The registry record does not report a multiplicity adjustment plan, a hierarchy for testing outcomes, or which secondary comparisons were intended to be confirmatory. It also does not report whether interim analyses were conducted. These details are not reported in the registry record, so the unadjusted p-values should not be interpreted as if family-wise error or another multiplicity concern had been addressed.

The registry record lists zero reported analysis entries. It therefore does not document the analysis populations, the handling of protocol deviations, or an intention-to-treat or per-protocol approach. The posted arm summaries give denominators for each outcome, but do not describe whether every randomized participant contributed to every analysis or why denominators may differ. Missing-data methods and the amount or pattern of missing outcome data are not reported in the registry record.

These omissions limit assessment of whether the comparisons followed the intended analysis plan and whether missingness could affect the results. They do not establish that analyses were inappropriate or that missing data occurred; the relevant methods and details are simply not reported. The posted comparisons are unadjusted recalculations from the available arm summaries and should be distinguished from a complete trial analysis.

The record also does not report a clinical importance threshold for the primary or secondary outcomes, or a prespecified strategy for handling multiple endpoints. That absence makes it difficult to distinguish a statistically notable result from a result that would matter in practice, and to assess how much emphasis any one secondary finding should receive. A careful interpretation should give priority to the defined primary endpoint, describe uncertainty, and treat unadjusted secondary comparisons cautiously.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: catheter-related blood stream infection (2.7%).

The posted serious adverse event figures list 2 affected participants in the long-axis, in-plane arm, and 0 in each of the short-axis, out-of-plane and oblique-axis, in-plane arms. The registry lists 75, 73, and 72 participants at risk in those respective arms. The serious-event term identified in the record is catheter-related blood stream infection, listed as 2.7%.

These are descriptive counts. Zero recorded serious events in an arm does not prove that the risk is absent, particularly when the number at risk is limited. The record does not provide a comparative statistical analysis of serious adverse events or enough detail to evaluate ascertainment, follow-up, or the relationship of each event to the procedure.

Other adverse events are listed separately: 5, 11, and 5 affected participants in the long-axis, short-axis, and oblique-axis arms, respectively. Deaths are not reported in the registry record. The adverse-event counts should not be confused with the listed secondary outcomes of mechanical and infectious complications, whose results are not reported in the registry record. The safety data are therefore a limited descriptive account, not a complete comparative safety analysis.

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

The results answer a specific registry question: how cannulation success, defined by guidewire placement within 180 seconds, was recorded across three ultrasound-guided approaches in this randomized parallel-group trial. The posted arm counts are similar, and the unadjusted risk-difference intervals for both comparisons with the long-axis approach include zero. The data do not establish a clear difference in this primary endpoint, but they also do not establish equivalence or rule out differences that could matter.

The endpoint is one part of procedural performance. Attempts, first-attempt cannulation, time, and complications address different features. The secondary summaries suggest that these aspects do not all move in the same way, and their interpretation is limited by unadjusted comparisons and the absence of a reported analysis hierarchy. The record does not provide numeric results for mechanical or infectious complications as secondary outcomes. Serious adverse-event counts are descriptive and cannot stand in for a complete safety comparison.

The findings apply to the participants and procedures represented in the trial record. The record does not report enough eligibility, setting, operator, or implementation detail to determine how directly the results extend to other contexts. It also does not describe the original statistical plan, missing-data handling, analysis populations, or sample-size justification. Those omissions constrain evaluation of the evidence but do not, by themselves, demonstrate that the trial was conducted improperly.

Statistical uncertainty and clinical importance are separate questions. The confidence intervals describe uncertainty in the estimated contrasts, while the registry does not report a threshold for a clinically important difference. A non-significant unadjusted p-value is not evidence that two approaches are identical, and a secondary p-value below a conventional threshold is not conclusive when multiplicity and prespecification are unclear.

Accordingly, the posted results should be read as a limited comparison of recorded procedural outcomes, not as medical advice or a definitive ranking of techniques. They do not demonstrate that any approach works or does not work, nor do they determine the best approach for an individual or setting. They show what was recorded in this trial and how uncertain the comparisons remain.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison and an apparently similar set of event counts are not enough to establish that two approaches are equivalent. The primary estimates are close to zero, but the intervals cover differences in either direction. Without a prespecified equivalence margin, a near-zero point estimate cannot answer whether the approaches are sufficiently similar for a particular clinical purpose.

It also highlights the distinction between an outcome definition and broader procedural performance. Success was explicitly tied to guidewire insertion within a time limit. Attempts and time describe other dimensions, and first-attempt success has its own definition as a secondary outcome. Reading these measures together can add context, but combining them informally would blur the trial’s distinct endpoints.

The posted secondary findings make multiplicity important. Several outcomes and two comparisons against a common reference are considered, yet no adjustment strategy or outcome hierarchy is reported. Unadjusted results can be informative as estimates, but isolated p-values across a collection of outcomes should not be treated as confirmatory evidence without knowing what was prespecified and how multiplicity was handled.

The record also demonstrates how registry completeness affects statistical interpretation. No reported analysis entries are listed, and details about missing data, analysis populations, interim analyses, and original sample-size justification are absent. Such omissions leave readers unable to connect the displayed estimates to a full protocol-based analysis. The planning calculations can illustrate how assumed effects relate to study size, but they cannot recover the trial’s original design reasoning.

For biostatisticians and clinical researchers, the central lesson is to keep the estimand, uncertainty, analysis plan, and reporting limitations in view together. An effect estimate is not a decision threshold; a confidence interval is not a guarantee; and secondary patterns do not erase the primary result. Transparent reporting of methods and outcomes is necessary to assess how much weight a trial’s numerical findings can bear.

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.

Several trial-specific limitations follow from what the registry record does not report. It describes the study as randomized and single-masked, but gives no further account of sequence generation, allocation concealment, or masking implementation. The record also does not give detailed eligibility criteria, the clinical setting, operator experience, or procedural standardization. These omissions make it difficult to judge possible sources of bias or the applicability of the results to other circumstances.

The registry reports no analysis entries. The analysis population, handling of deviations from assigned technique, and approach to missing outcomes are not reported in the registry record. Although outcome-specific denominators are posted, the record does not explain the analysis flow or whether all randomized participants contributed to each result. The original sample-size justification and planned statistical methods are likewise not reported.

The primary comparisons are unadjusted recalculations, and the registry does not describe a multiplicity plan for the several secondary outcomes and comparisons. This is particularly relevant when interpreting nominal p-values for secondary measures. There is also no reported threshold for clinically important differences, so statistical estimates cannot be mapped to a stated clinical margin.

Only three of the listed secondary outcomes have numeric results posted: attempts, first-attempt cannulation, and time. Results for mechanical and infectious complications as secondary outcomes are not reported in the registry record. The adverse-event section provides counts but does not report a full comparative analysis or details on ascertainment and follow-up. Deaths are not reported in the registry record.

Finally, the registry entry’s description of the oblique-arm technique is truncated, and its detailed procedural description is therefore incomplete in the record. These limitations do not show that the methods were flawed; they identify what cannot be evaluated from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Three Techniques for Ultrasound-guided Internal Jugular Cannulation — NCT01966354.
• Registry record last updated 2016-08-01; status last verified 2016-06.
• Results first posted 2016-06-28.
• 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 a completed, randomized, single-masked, parallel-group trial of three ultrasound-guided internal jugular cannulation approaches. Enrollment is listed as 220. The primary endpoint was guidewire placement within 180 seconds, classified as successful or unsuccessful.

The posted primary counts were 73 of 75 for long-axis, in-plane; 71 of 73 for short-axis, out-of-plane; and 68 of 72 for oblique-axis, in-plane. Both unadjusted risk-difference intervals against the long-axis approach include zero. The record also posts numeric results for attempts, first-attempt cannulation, and time. Secondary results for mechanical and infectious complications are not reported in the registry record.

Analysis populations, missing-data methods, the original sample-size justification, and a multiplicity plan are not reported in the registry record. The findings are best read as estimates with uncertainty and as a limited account of the posted outcomes, not as proof of equivalence or a complete comparative safety analysis.