Dexmedetomidine for Sedation of Endobronchial Ultrasound-guided Transbronchial Needle Aspiration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dexmedetomidine for Sedation of Endobronchial Ultrasound-guided Transbronchial Needle Aspiration (NCT03521505), a randomized phase 4 study. The primary outcome is Hypoxemia During Maintenance.

2. Clinical Question

3. Trial Design

The registry identifies NCT03521505 as a completed, phase 4, randomized, parallel-group trial sponsored by Chang Gung Memorial Hospital. The trial compared dexmedetomidine with propofol for sedation during EBUS-guided transbronchial needle aspiration. It lists an enrollment of 50 and reports 25 participants in each arm for the primary outcome. The allocation is described as randomized; masking is listed as none.

The registry dates the study start to 2018-05-11 and primary completion to 2020-01-22. These dates describe the study record, but do not establish how long each participant was followed beyond the timeframes attached to individual outcomes. For the primary outcome, observation began after bronchoscopy started and continued up to 120 minutes. Secondary outcomes have their own stated timeframes.

The interventions were drug-based sedation: dexmedetomidine in one arm and propofol in the other. The record lists Bronchoscopy as the condition. It does not report the randomization sequence, allocation concealment, detailed eligibility criteria, sedation dosing, co-interventions, or a protocol description beyond the intervention summaries. The original sample-size rationale and the trial's prespecified statistical analysis plan are not reported in the registry record.

The primary outcome was hypoxemia during maintenance of bronchoscopic sedation. The listed secondary outcomes address hypoxemia during induction, global tolerance for bronchoscopy, cooperation as judged by bronchoscopists, hypotension, bradycardia, and procedure and recovery time. The registry lists seven outcome measures in total, while the posted results include the primary outcome and three secondary outcome comparisons. Results for the other listed secondary outcomes are not reported in the registry record.

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: 50 subjects met inclusion criteria and were randomized to treatment.

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 Hypoxemia During Maintenance, measured over After starting bronchoscopy, up to 120 minutes.

The primary endpoint counts participants with hypoxemia during maintenance of bronchoscopic sedation. The registry defines hypoxemia as oxyhemoglobin saturation (SpO2) <90%. Its timeframe begins after bronchoscopy starts and extends up to 120 minutes. The reported outcome is a count of participants with the event, rather than a continuous measure of oxygen saturation or a count of repeated episodes.

Counting participants who cross a defined threshold provides a clinically interpretable summary of whether the event occurred during the specified period. It also allows the event frequency to be compared between the sedation arms. The endpoint therefore focuses on an adverse respiratory event during the procedure, consistent with the registry summary's stated interest in preventing hypoxemia during bronchoscopic sedation. That rationale explains the outcome's relevance, but does not itself establish which arm had a better result or whether any observed difference was caused by the sedative.

The posted counts are 8 participants in the dexmedetomidine arm and 14 in the propofol arm, with 25 participants reported in each arm for this outcome. The record does not describe how oxygen saturation was monitored, how long an episode had to last to meet the definition, or how repeat episodes were handled. Those measurement details are not reported in the registry record.

7. Results Posted in the Registry

• Propofol Arm: 56.0% (14/25) versus 32.0% (8/25) on control; risk difference 24.0 percentage points (95% CI -2.7 to 50.7), risk ratio 1.75 (0.90–3.42); unadjusted two-proportion z-test p = 0.087.

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.

Hypoxemia During Induction

• 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:
  • Propofol Arm: 8.0% (2/25) versus 4.0% (1/25) on control; risk difference 4.0 percentage points (95% CI -9.1 to 17.1), risk ratio 2.00 (0.19–20.67); unadjusted two-proportion z-test p = 0.552.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Propofol Arm and the control. The interval gives the range of effects that remain compatible with the data.

Hypotension During Bronchoscopic Sedation

• 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:
  • Propofol Arm: 20.0% (5/25) versus 4.0% (1/25) on control; risk difference 16.0 percentage points (95% CI -1.5 to 33.5), risk ratio 5.00 (0.63–39.79); unadjusted two-proportion z-test p = 0.082.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Propofol Arm and the control. The interval gives the range of effects that remain compatible with the data.

Bradycardia During Bronchoscopic Sedation

• 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:
  • Propofol Arm: 16.0% (4/25) versus 48.0% (12/25) on control; risk difference -32.0 percentage points (95% CI -56.3 to -7.7), risk ratio 0.33 (0.12–0.89); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Propofol Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover events during induction or sedation, as well as patient tolerance, bronchoscopist-rated cooperation, and procedure and recovery time. The posted numerical comparisons cover hypoxemia during induction, hypotension during bronchoscopic sedation, and bradycardia during bronchoscopic sedation. Results for tolerance, cooperation, and procedure and recovery time are not reported in the registry record.

Across the three posted secondary comparisons, the direction is not uniform: the recorded counts for induction hypoxemia and hypotension are higher in the propofol arm, whereas bradycardia is higher in the dexmedetomidine arm. This pattern is consistent with the outcomes capturing different aspects of sedation rather than a single common response. It also means that secondary findings should not be compressed into a claim that one arm was uniformly better across all outcomes.

The primary result concerns hypoxemia during maintenance. Induction hypoxemia addresses a separate phase, and hypotension and bradycardia are different safety outcomes. Those secondary outcomes provide context for the broader comparison, but they do not change the primary endpoint's definition or resolve its uncertainty. Nor do they substitute for outcomes whose results are not posted.

Each secondary comparison is unadjusted, and the registry record does not describe a prespecified hierarchy or correction for testing multiple outcomes. In general, examining multiple outcomes makes isolated small p-values less persuasive unless the analysis plan accounts for multiplicity. The secondary p-values should therefore be treated as descriptive signals in this record, not as independent confirmatory evidence. Their estimates and intervals also need to be read with the small arm-level outcome counts and the uncertainty they imply.

The full secondary-outcome picture is incomplete: several listed domains have no posted results, and no analysis descriptions are listed. This limits the ability to assess whether the visible secondary pattern reflects the intended reporting plan or how the outcomes were assessed. The results can describe the posted endpoints, but they cannot establish a single overall treatment effect across all aspects of the procedure.

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

• Hypoxemia During Induction
• The Global Tolerance for Bronchoscopy
• The Cooperation of Patients From the View of Bronchoscopists
• Hypotension During Bronchoscopic Sedation
• Bradycardia During Bronchoscopic Sedation
• Procedure Time and Recovery Time

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the hypoxemia definition during the stated maintenance timeframe or did not. The reported counts are 8 of 25 in the dexmedetomidine arm and 14 of 25 in the propofol arm. Because the outcome is a count of participants with an event, the comparison is framed in terms of event risks rather than averages of a continuous measurement.

What does a risk difference describe?

In general, a risk difference subtracts the event risk in one group from the event risk in the other. Here the comparison is propofol relative to dexmedetomidine, so a positive risk difference corresponds to a larger observed event risk in the propofol arm. The posted estimate is 0.24. This absolute-scale measure communicates the size of the contrast in event frequency without converting it into a relative multiplier. It should be read alongside its interval, because a point estimate alone does not convey how uncertain the comparison is.

How do relative risk and odds ratio differ?

In general, the relative risk divides one group's event risk by the other group's event risk. The odds ratio compares event odds rather than event risks. Both express a relative contrast, while the risk difference expresses an absolute contrast. The registry posts a relative risk of 1.75 and an odds ratio of 2.705 for the primary comparison. These measures can be useful for different purposes, but neither removes the uncertainty in the observed data. They are transformations of the same group results, not separate replications.

What does the interval add?

In general, a confidence interval describes the range of effect estimates that are reasonably compatible with the data under the method used to calculate it. A narrow interval indicates greater precision than a wide one. The primary risk-difference interval runs from -0.027 to 0.507, crossing zero. The relative-risk interval runs from 0.897 to 3.416, and the odds-ratio interval runs from 0.854 to 8.568. Each spans values consistent with no contrast as well as values pointing toward a difference. The confidence level and exact interval method are not reported in the registry record, so those details should not be assumed.

What does the p-value say?

In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and analysis procedure. It is not the probability that the null model is true, and it is not a measure of clinical importance. The primary unadjusted p-value is 0.087. The registry record does not report the analysis procedure or the threshold selected for the primary comparison. The posted p-value can therefore be described, but should not be given an interpretation as a prespecified pass-or-fail decision.

What is the role of randomization?

In general, random allocation can help balance known and unknown baseline factors across study arms, reducing confounding in the comparison when the trial is conducted and analyzed appropriately. The registry labels this study randomized and parallel-group. It does not report sequence generation, allocation concealment, adherence, crossovers, or a participant flow account. Those details matter when assessing how well randomization protected the comparison and whether the posted outcome counts reflect the intended analysis population.

Why do unadjusted comparisons need care?

In general, testing many outcomes increases the chance that at least one result appears noteworthy by chance. A multiplicity plan can address that issue by defining how results across outcomes or analyses are to be interpreted. The registry lists several secondary outcomes, and the posted secondary comparisons are unadjusted. A correction or hierarchy is not reported in the registry record. The secondary p-values should consequently be interpreted as descriptive evidence, not as a set of confirmatory tests with controlled overall error.

The posted comparisons are simple, unadjusted calculations from the group summaries. They do not substitute for a detailed trial analysis plan. The registry reports no analyses in its analysis listing, and the analysis methods, handling of missing outcomes, and analysis population are not reported in the registry record. It is therefore important to distinguish the group counts and calculated contrasts from a sponsor-reported adjusted or prespecified analysis.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of 0.24 for propofol relative to dexmedetomidine. Its interval, -0.027 to 0.507, is wide enough to include zero and effects in either direction. The data therefore do not pin down the size or direction of the underlying contrast with much precision. The interval should be considered together with the point estimate: the point estimate favors a higher observed event risk in the propofol arm, while the range of compatible values remains broad.

The relative measures tell a similar uncertainty story. The relative risk is 1.75, with an interval from 0.897 to 3.416; the odds ratio is 2.705, with an interval from 0.854 to 8.568. Both intervals include the value corresponding to no relative difference. The point estimates should not be read as established effects when their intervals remain compatible with no contrast.

In general, precision depends partly on the amount of information in the outcome data and the frequency of the event. The primary outcome has 25 participants reported per arm and a modest number of recorded events in each arm. With limited information, estimated contrasts can remain uncertain even when the point estimates appear different. This is a statistical explanation, not a claim about the original trial's design rationale.

The registry does not state the confidence level or interval-calculation method. The interval limits are reproduced as posted, without assigning a confidence level that is not documented. The unadjusted p-value of 0.087 also does not replace the interval: the p-value gives a test summary under a null model, whereas the interval communicates uncertainty about a range of effect values. Together, these statistics support a cautious reading rather than a definite conclusion about the primary comparison.

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 planning figures concern participants per arm for these binary participant-count outcomes; they are not total-event counts. The time-to-event convention of reporting total events does not apply to these outcomes. The figures are planning illustrations based on the observed effect, not the trial's original design assumptions. The original design assumptions are not reported in the registry record.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The entries for 100% of the observed effect use the observed contrast as the planning target; entries for 75% and 50% use progressively smaller target effects. Smaller effects require more participants per arm to detect under the same assumptions.

In plain language, 80% power means that, if the assumed effect and planning model were correct, a study designed at that level would have an 80% chance of detecting the target effect under the specified testing framework. The 90% power column expresses a higher chance of detecting that same target effect, and therefore gives larger participant requirements under the same assumptions. These are design calculations, not a report of what happened in the completed trial.

This is not observed power. It does not measure the probability that the trial's result is correct, and it cannot repair the uncertainty in the observed estimate. The planning values also do not show that the original trial was designed using these assumptions; they are separate illustrations derived from the posted effect. Because the primary estimate itself is uncertain, planning a future study around a fraction of that estimate would also require judgment about what effect is meaningful and plausible.

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 = 0.320; treatment proportion p₁ = 0.560; average p̄ = 0.440.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7020 = 1.3759.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6812 = 0.5733.
4. n = (1.3759 + 0.5733)² / (0.2400)² = 66.0, rounded up to 66 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 <- 0.32                          # control proportion
p1 <- 0.56                          # 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(3521505)
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 = 66 (80% power), 88 (90% power)
 75% of observed effect: n per arm = 117 (80% power), 155 (90% power)
 50% of observed effect: n per arm = 256 (80% power), 342 (90% power)
power.prop.test: 66 
Simulated power at n = 66 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 lists multiple outcomes: one primary endpoint and six secondary outcome domains. The posted secondary results include three comparisons, while results for tolerance, cooperation, and procedure and recovery time are not reported in the registry record. The record does not specify whether all outcomes were prespecified in a protocol, how any outcome hierarchy was defined, or whether a multiplicity adjustment was planned or performed.

In general, multiplicity matters because repeated testing across endpoints can raise the chance of at least one apparently unusual result even when there is no real effect. A prespecified hierarchy, adjusted significance criteria, or a clearly exploratory framing can help readers distinguish confirmatory from descriptive findings. None of those analysis details is reported in the registry record. The posted secondary p-values are unadjusted, so they should be interpreted cautiously and in the context of the whole set of planned outcomes, not selectively.

The record also does not report how missing outcome data were handled, whether every randomized participant contributed to each analysis, or which analysis population was used. It does not provide a participant flow account, reasons for any missing measurements, or an intention-to-treat or per-protocol designation. These omissions prevent assessment of whether the reported counts include all randomized participants or whether exclusions or missing observations could affect the comparisons.

No analysis descriptions are listed for the secondary outcomes, and the registry does not provide a detailed statistical analysis plan for the primary endpoint. The exact test procedures, interval methods, covariate adjustments, and any planned subgroup analyses are not reported in the registry record. As a result, the posted unadjusted comparisons are useful descriptive summaries, but cannot be checked against a documented prespecified analytic strategy.

These reporting gaps do not show that missing data or selective reporting occurred. They mean that the registry record does not permit readers to evaluate those possibilities. Interpretation should accordingly focus on the outcome counts and uncertainty that are posted, while treating unreported analysis and data-handling decisions as unknown.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoxemia (56.0%), hypotension (20.0%).

The registry reports serious adverse event counts for each arm. In the dexmedetomidine arm, 9 participants were reported as affected by serious adverse events, with 25 at risk; in the propofol arm, 17 were reported as affected, with 25 at risk. The registry lists 0 deaths in each arm. These are arm-level registry counts and should be distinguished from the primary outcome counts, which specifically concern hypoxemia during maintenance.

The record also reports other adverse event counts: 16 affected participants in the dexmedetomidine arm and 18 in the propofol arm, with 25 at risk in each arm. Hypoxemia and hypotension are the top serious adverse event terms listed, at 56.0% and 20.0%, respectively. Those terms are registry summaries; the record does not provide enough detail to attribute each event to a particular arm or to determine whether events overlap.

In general, adverse-event counts describe events recorded during a study, but by themselves do not establish causation. The registry does not report detailed event narratives, severity grading beyond the serious-event classification, timing, or attribution decisions. The counts should therefore be read as safety reporting, not as proof that an intervention caused or prevented an event.

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

The posted primary data show fewer participants with hypoxemia during maintenance in the dexmedetomidine arm than in the propofol arm: 8 versus 14, with 25 participants reported in each arm. The estimated risk difference is 0.24 for propofol relative to dexmedetomidine, but its interval from -0.027 to 0.507 spans zero. The point estimate describes the observed direction; the interval indicates that the underlying contrast remains uncertain.

This result does not establish that either sedative is more effective or safer overall. The primary endpoint captures a defined event during a specific phase of one procedure, and the registry does not report a comprehensive clinical outcome assessment. The secondary results point in different directions across outcomes, and several listed secondary domains have no posted results. The serious adverse-event counts also require cautious interpretation because detailed event attribution and timing are not reported.

The findings apply most directly to the trial record's context: sedation for EBUS-TBNA, comparison of dexmedetomidine with propofol, and the stated outcome windows. The record does not provide detailed eligibility criteria or a participant profile that would support claims about broader populations or other procedures. Generalizing beyond the recorded study context would require evidence not contained in this registry record.

The unadjusted p-value of 0.087 is one summary of the primary comparison, not a probability that the observed effect is true or false. The record does not report the prespecified primary analysis threshold, interval method, missing-data handling, or analysis population. Those omissions further limit how strongly the result can be interpreted as a formal confirmatory finding.

The most defensible reading is descriptive: an observed difference in event counts, with substantial uncertainty and incomplete detail about analysis and outcome reporting. The data neither demonstrate equivalence nor settle whether a meaningful difference exists. They identify a comparison and an outcome pattern that require interpretation alongside the trial's limited size, the interval estimates, and the registry's reporting gaps.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an observed contrast and a precise estimate. The primary event counts differ between arms, and the point estimate is not zero. Yet the risk-difference interval includes zero and extends to a sizeable positive value. A visible difference in the sample should not be mistaken for a settled estimate of the underlying contrast.

The study also shows why absolute and relative measures are often read together. The risk difference describes the absolute event-frequency contrast, while the relative risk and odds ratio describe relative contrasts. Their estimates use the same group data, and the intervals for each remain broad. Consistency across measures in the direction of their point estimates does not remove the uncertainty shared by those estimates.

Secondary outcomes add another statistical lesson: outcomes can move in different directions, and a collection of unadjusted comparisons is not equivalent to a single, prespecified overall test. Here, the secondary pattern varies across events, while the multiplicity plan and several outcome results are not reported. That makes restraint important when moving from endpoint-specific observations to an overall interpretation.

Finally, the planning illustrations distinguish design questions from retrospective descriptions. They show how required participant numbers change when the target effect is made smaller, under stated assumptions. They are not observed power and do not reveal the original design rationale. Keeping planning calculations, posted results, and undocumented trial methods separate helps readers avoid treating one as evidence for another.

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 primary comparison is based on 25 participants reported per arm, and the interval estimates are broad. This limits precision for the hypoxemia contrast. The registry does not report eligibility criteria, baseline characteristics, dosing details, or procedural and monitoring protocols, so it is difficult to judge how consistently the intervention and outcome definitions were applied or how directly the findings may relate to other settings.

Masking is listed as none. The record does not explain whether outcome assessment was blinded or whether objective monitoring procedures reduced the possibility of assessment differences. It also does not report randomization sequence generation or allocation concealment. These details are important for evaluating potential bias, but their absence from the record is not evidence that a particular bias occurred.

Analysis reporting is limited. The primary statistical plan, interval method, missing-data approach, and analysis population are not reported in the registry record. The secondary comparisons are unadjusted, and no multiplicity strategy is reported. Several listed secondary outcomes have no posted results, which leaves the secondary picture incomplete and makes it difficult to assess the full reporting plan.

The registry's safety summaries provide counts and selected serious-event terms but not detailed timing, attribution, severity information beyond the serious classification, or event-level descriptions. The counts therefore cannot establish causation or provide a complete assessment of the safety profile. The record also does not give enough participant-flow detail to determine whether any outcome data were missing or whether all randomized participants were included in each comparison.

These limitations are specific to what the registry record reports. They should be treated as unresolved information gaps, not as proof of protocol deviations, selective reporting, or biased conduct.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dexmedetomidine for Sedation of Endobronchial Ultrasound-guided Transbronchial Needle Aspiration — NCT03521505.
• Registry record last updated 2021-09-09; status last verified 2021-08.
• Results first posted 2021-09-09.
• 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

NCT03521505 is a completed phase 4 randomized, open-label parallel-group trial sponsored by Chang Gung Memorial Hospital. It compared dexmedetomidine with propofol for sedation during EBUS-guided transbronchial needle aspiration. The registry lists enrollment of 50 and reports 25 participants per arm for the primary outcome.

The primary endpoint was hypoxemia during maintenance, defined as SpO2 <90% after bronchoscopy started and up to 120 minutes. The posted counts were 8 in the dexmedetomidine arm and 14 in the propofol arm. The risk-difference estimate was 0.24, with an interval from -0.027 to 0.507 and an unadjusted p-value of 0.087.

Secondary results show differing directions across outcomes, while several listed secondary results and key analysis details are not reported in the registry record. The primary estimate is uncertain and should be interpreted as a description of the posted data, not a definitive overall comparison.