Prospective Trial of EUS-FNA Versus EUS-FNB Using a Novel Core Biopsy Needle: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prospective Trial of EUS-FNA Versus EUS-FNB Using a Novel Core Biopsy Needle (NCT01769248), a randomized na study. The primary outcome is Diagnostic Yield of EUS-FNB and EUS-FNA.

2. Clinical Question

The trial addresses whether the diagnostic yield recorded for the two sampling approaches differs. The primary outcome is the percentage of patients in whom a diagnosis was achieved, with the outcome timeframe listed as 1 year. The registry describes EUS as a way to obtain cellular material by aspiration or tissue for biopsy and histologic analysis. The clinical question is therefore about the yield of these approaches in the enrolled trial, not about every possible use of the procedures or every type of lesion.

The posted primary results report diagnostic yield of 67.1% for fine needle aspiration and 90.0% for fine needle biopsy, with 70 participants listed for each approach. These are the observed proportions in this trial record. They do not by themselves establish how the procedures would compare in other populations or clinical settings. The registry lists three conditions but does not report a detailed participant description or outcome results by condition. The question also concerns diagnostic yield, not patient outcomes beyond diagnosis, and should be interpreted within that scope.

3. Trial Design

NCT01769248 is listed as a randomized, prospective crossover trial comparing EUS-FNA with EUS-FNB using a novel core biopsy needle. The registry names Northwestern University as sponsor and gives the status as completed. The listed enrollment is 140. The start is recorded as 2012-09 and primary completion as 2014-02. The phase is listed as not applicable.

The two interventions are fine needle aspiration and fine needle biopsy. The trial model is crossover, and masking is listed as none. The registry's primary result lists 70 participants for each procedure. The record also describes a secondary outcome concerning diagnosis after crossover, with results reported for the sequence groups. It does not provide enough detail to reconstruct all procedural steps, the timing of each crossover, or the criteria determining which participants crossed over. Those details are not reported in the registry record.

The primary endpoint is diagnostic yield, expressed as the percentage of patients with a diagnosis, and its timeframe is 1 year. The two other posted outcomes concern specimen adequacy assessed by rapid-onsite evaluation and the percentage of patients in whom a diagnosis was achieved after crossover. The registry reports no statistical analyses under its analyses listing. It also does not report the trial's original sample-size justification, planned statistical analysis, interim analyses, or allocation procedures beyond randomized assignment. Those omissions limit what can be concluded about how the study was planned and how the reported comparisons were selected or conducted.

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 Diagnostic Yield of EUS-FNB and EUS-FNA, measured over 1 year.

The primary endpoint measures the percentage of patients for whom EUS-FNB provides a final diagnosis of the sampled lesion. The registry's description identifies diagnostic yield as the primary outcome, with the timeframe listed as 1 year. The results also give the corresponding yield for EUS-FNA, allowing the two approaches to be described side by side.

Diagnostic yield is useful for this question because it summarizes whether a sampling procedure produced enough diagnostic information to reach a diagnosis. It is a binary outcome at the participant level: a participant either had a diagnosis achieved or did not, and the group result is expressed as a percentage. This makes the endpoint directly interpretable as a proportion of participants, while still depending on how the trial defined an achieved diagnosis and assessed it.

The registry describes fine needle aspiration as obtaining cells and fine needle biopsy as obtaining tissue for histologic analysis. The endpoint captures the diagnostic result rather than the quantity or microscopic characteristics of the specimen alone. Specimen adequacy is posted separately as a secondary outcome. The record does not give further operational criteria for a final diagnosis, describe independent adjudication, or specify how missing endpoint observations were handled. As a result, the stated endpoint and percentages can be interpreted as registered, but those additional measurement details are not reported in the registry record.

7. Results Posted in the Registry

• Fine Needle Biopsy: 90.0% (63/70) versus 67.1% (47/70) on control; risk difference 22.9 percentage points (95% CI 9.8 to 35.9), risk ratio 1.34 (1.12–1.61); unadjusted two-proportion z-test p = <0.001.

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.

Specimen Adequacy as Assessed by Rapid-onsite Evaluation of FNA and FNB

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fine Needle Biopsy: 82.9% (58/70) versus 60.0% (42/70) on control; risk difference 22.9 percentage points (95% CI 8.4 to 37.3), risk ratio 1.38 (1.11–1.72); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Fine Needle Biopsy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Patients in Whom a Diagnosis is Achieved After Crossover (%)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fine Needle Biopsy to Fine Needle Aspiration: 41.7% (5/12) versus 96.4% (27/28) on control; risk difference -54.8 percentage points (95% CI -83.5 to -26.0), risk ratio 0.43 (0.22–0.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Fine Needle Biopsy to Fine Needle Aspiration than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address related but distinct parts of the diagnostic process. Specimen adequacy concerns whether the sample was adequate under rapid-onsite evaluation, whereas the primary endpoint concerns whether a diagnosis was achieved. The post-crossover outcome focuses on diagnosis after participants moved between procedures. Together, these measures provide additional context around the primary diagnostic-yield comparison, but they do not measure the same endpoint or necessarily involve the same participants.

The overall pattern is consistent with the primary result in that the posted specimen-adequacy comparison also favors fine needle biopsy. The crossover outcome is reported for sequence groups and has a different structure and participant count from the main comparison. That result should not be treated as a direct substitute for the primary endpoint: the groups reflect crossover sequences, and the registry does not explain how participants entered the crossover analysis or how the comparison was modeled.

The registry reports unadjusted p-values for the posted comparisons, while its analysis listings contain no reported analyses. No multiplicity procedure is described. When several outcomes are examined, unadjusted results carry less weight as confirmatory evidence because the probability of finding at least one apparently notable result can rise with the number of comparisons. This is a general statistical concern; it does not invalidate a secondary result, but it does call for attention to prespecification, analysis methods, and consistency with the primary question.

Secondary findings are best used to help characterize the trial rather than to expand the primary conclusion beyond its endpoint. The registry does not report whether these secondary outcomes were prespecified as confirmatory, whether they were adjusted for baseline or design features, or how missing observations were treated. Their relationship to the primary result is therefore descriptive, with the primary endpoint remaining the central registered comparison.

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

• Specimen Adequacy as Assessed by Rapid-onsite Evaluation of FNA and FNB
• Percentage of Patients in Whom a Diagnosis is Achieved After Crossover (%)

9. Statistical Interpretation

10. Statistical Methods Explained

What does diagnostic yield mean?

Diagnostic yield is the proportion of participants for whom the sampling procedure resulted in a diagnosis. For a binary outcome, each participant contributes to one of two outcome categories: diagnosis achieved or not achieved. The reported percentage describes the observed proportion in the relevant group. It is a summary of the endpoint as recorded, not a measure of how certain any individual diagnosis is.

What is a risk difference?

The risk difference compares the two outcome proportions by expressing their absolute separation on the proportion scale. In this comparison, the stated value is 0.229 for fine needle biopsy relative to fine needle aspiration. The confidence interval for that difference runs from 0.098 to 0.359. A value above zero indicates that the observed proportion is higher in the biopsy group under the stated comparison direction. The interval communicates uncertainty around the estimated difference; it does not describe the range of individual participant outcomes.

How do relative risk and odds ratio differ?

The relative risk compares the probability of the outcome in one group with the probability in the other. The posted relative risk is 1.34, with a 95% confidence interval from 1.118 to 1.607. The odds ratio instead compares odds, where odds are the probability of an outcome relative to the probability of no outcome. The posted odds ratio is 4.404, with a 95% confidence interval from 1.744 to 11.12. These measures use different scales, so their numerical values should not be compared as though they represented the same quantity. When outcomes are common, an odds ratio can be farther from 1 than the corresponding relative risk; this is a general statistical feature, not a separate finding about the trial.

What does a confidence interval convey?

A confidence interval gives a range of values compatible with the observed estimate under the statistical model and repeated-sampling framework used to construct it. It is a way to express precision: narrower intervals indicate less statistical uncertainty than wider intervals on the same scale. A confidence interval does not account for every possible source of error. In particular, it cannot correct an unclear endpoint definition, bias in measurement, incomplete follow-up, or a mismatch between the analysis and the trial design.

How should the p-value be read?

The primary comparison has an unadjusted p-value of <0.001. A p-value measures how unusual the observed evidence, or evidence more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it quantify the probability that a result will replicate. The term unadjusted indicates that the posted value has not been adjusted for multiplicity in the displayed result. The registry does not describe a multiplicity procedure.

Why does crossover design matter?

In a crossover design, participants may receive or be assessed under more than one intervention in a sequence. This can allow within-participant comparisons, but it also means that the statistical analysis may need to account for the relationship between observations from the same participant and for sequence or period effects. This is general statistical context. The registry identifies a crossover model and posts a separate outcome after crossover, but does not report the primary analysis method, the handling of sequence and period, or whether the primary comparison used paired observations. Those methods are not reported in the registry record, so no specific paired or independent analysis should be inferred from the design label alone.

What is the role of secondary outcomes?

Secondary outcomes add context to the primary result by describing specimen adequacy and diagnoses achieved after crossover. They can help characterize different aspects of performance, but they are not interchangeable with the primary endpoint. Secondary comparisons may be less conclusive when they involve fewer participants, are not adjusted for multiple testing, or were not designated as confirmatory. General statistical reasoning calls for caution when many outcomes or comparisons are assessed, since the chance of at least one apparently unusual result can increase. The registry lists no reported analysis entries and does not state how secondary analyses were planned.

What can the outcome summaries establish?

The posted percentages and comparison measures describe the registry's observed results. They do not establish that the procedures were compared using a particular model, that all randomized participants contributed to each endpoint, or that the reported confidence intervals account for the crossover structure. The original analysis plan, population definitions, missing-data methods, and interim analysis procedures are not reported in the registry record. Interpretation should therefore distinguish the arithmetic meaning of the posted effect estimates from the unanswered questions about their analytic construction.

11. Confidence Intervals and Precision

The primary result reports a risk difference of 0.229 for fine needle biopsy compared with fine needle aspiration. Its 95% confidence interval extends from 0.098 to 0.359. This interval excludes zero, which is consistent with the reported unadjusted p-value of <0.001 for the comparison. The point estimate gives the central estimated contrast; the interval shows a range of values compatible with the data and analysis assumptions.

The interval is informative about sampling precision, but it should not be read as covering all forms of uncertainty. The registry does not describe the statistical model used to construct it, the handling of the crossover structure, or the analysis population. If those features affect the analysis, they can affect how the interval should be interpreted. Confidence intervals also do not address selection, outcome measurement, or incomplete follow-up unless the methods specifically account for them.

The relative risk and odds ratio have their own intervals: 1.34 with a 95% confidence interval from 1.118 to 1.607 for relative risk, and 4.404 with a 95% confidence interval from 1.744 to 11.12 for odds ratio. Because these measures use different scales, the width and location of each interval should be interpreted on its own scale. The absolute risk difference is often more straightforward for understanding the separation between the observed proportions.

The trial includes 70 participants per procedure in the posted primary outcome. This is the reported group size, not a guarantee of high precision for every possible outcome or subgroup. The registry does not report subgroup intervals or condition-specific comparisons. Precision for the overall primary estimate should not be assumed to apply equally to any unreported subgroup or to a different 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 displayed planning estimates are illustrations based on the observed effect, not a description of the trial's original design calculation. For the posted non-time-to-event outcomes, the figures are participants per arm, rather than a total across both arms. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column indicates the illustrative number of participants per arm that would give an 80% chance of detecting the chosen effect under those assumptions, if the assumed effect and statistical model were correct. The 90% power column gives the corresponding planning figure for a 90% chance. These are planning probabilities under specified assumptions, not guarantees about a future study's result. The trial's own sample-size justification and original design assumptions are not reported in the registry record.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. As the effect being planned for becomes smaller, the estimated number of participants per arm increases. This follows a general statistical principle: smaller differences are harder to distinguish from random variation, so more information is usually needed to detect them with the same planned power and significance level.

These estimates are not observed power. They are hypothetical planning illustrations that reuse the observed effect as a starting point, and they should not be taken as evidence that the trial had a particular probability of detecting its result. The sample-size figures are also dependent on the stated assumptions; a different analysis, allocation, effect, or significance level could yield different planning requirements.

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 = 0.671; treatment proportion p₁ = 0.900; average p̄ = 0.786.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5803 = 1.1373.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5573 = 0.4691.
4. n = (1.1373 + 0.4691)² / (0.2286)² = 49.4, rounded up to 50 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 <- 0.671428571428571                          # control proportion
p1 <- 0.9                          # 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(1769248)
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 = 50 (80% power), 66 (90% power)
 75% of observed effect: n per arm = 98 (80% power), 130 (90% power)
 50% of observed effect: n per arm = 237 (80% power), 317 (90% power)
power.prop.test: 49.4 
Simulated power at n = 50 per arm: 0.821 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, subgroups, or analyses are evaluated. Even when each test uses a conventional threshold, testing many hypotheses can increase the chance that at least one result appears statistically notable by chance. Statistical plans sometimes address this with a prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory analyses. The registry lists a primary outcome and two secondary outcomes, but does not report a multiplicity strategy or identify which secondary findings, if any, were intended as confirmatory.

The posted comparison p-values are unadjusted. They therefore describe the individual comparisons as posted and should not be read as if a family-wide multiplicity adjustment had been applied. The registry's analysis listing contains no reported analyses, and the original statistical plan is not reported in the registry record. No specific adjustment method, testing sequence, or interim analysis procedure can be inferred.

The registry also does not describe missing-data handling or the populations used for the analyses. It does not state whether all randomized participants were included, whether the analysis followed an intention-to-treat principle, how protocol deviations were treated, or how participants with incomplete outcome information were handled. The listed denominators describe the groups for the reported outcomes, but do not answer those population-definition questions.

These omissions matter for interpreting a crossover trial. The record does not say whether analyses accounted for within-participant correlation, treatment sequence, period effects, or possible carryover. These are general design considerations rather than claims about what occurred. Without a reported methods description, the analysis cannot be independently matched to the design from the registry summary alone. The result remains interpretable as the posted comparison, but the strength of conclusions about confirmatory testing, missingness, and population handling is limited.

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.

For both fine needle aspiration and fine needle biopsy, the registry lists 70 participants at risk for serious adverse events and 0 affected. It also lists 70 at risk for other adverse events and 0 affected in each group. These entries mean that no events are recorded in those categories in the posted results for the listed groups.

Zero recorded events should not be interpreted as proof that an intervention has no risk. The registry does not provide detailed adverse-event definitions, surveillance methods, timing, or information about how completely events were collected. It also does not list death counts; those are not reported in the registry record. The safety entries therefore describe what was recorded, not a comprehensive estimate of all possible harms or a guarantee that no event occurred outside the reporting categories.

The adverse-event figures should be considered in the context of the listed participant counts and the limits of registry reporting. They do not establish a difference in safety between procedures, and they do not support medical advice for an individual patient.

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

The posted results show a higher observed diagnostic yield for fine needle biopsy than for fine needle aspiration in this randomized crossover trial. The primary proportions are 90.0% and 67.1%, respectively, and the reported risk difference is 0.229, with a 95% confidence interval from 0.098 to 0.359. The unadjusted p-value is <0.001. Taken together, these statistics describe a clear difference in the registry's primary comparison, while still leaving uncertainty about its exact size and the methods used to estimate it.

This comparison does not by itself establish how the procedures would perform across all lesions, institutions, or patient groups. Although the record lists pancreatic cancer, lymphadenopathy, and gastrointestinal stromal tumor among the conditions, it does not report results separately by condition. The trial's crossover design is also relevant, but the registry does not describe the primary analysis method in enough detail to assess how the analysis accounted for that design.

Diagnostic yield is not the same as every aspect of clinical benefit. The posted primary outcome concerns whether a diagnosis was achieved; it does not report longer-term patient outcomes or establish how the result affected subsequent care. The registry also does not provide detailed definitions of a final diagnosis or missing-data methods. The observed percentages should therefore be understood as endpoint results, not as a complete account of procedure performance or patient outcomes.

The adverse-event record lists zero serious and zero other adverse events in each group among the participants at risk, but event definitions and collection methods are not described. These entries do not show that there is no risk. Overall, the record supports a comparison of the reported outcomes in this trial; it does not settle broader questions that were not measured or reported.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it compares two diagnostic sampling approaches using a randomized crossover design and reports both an absolute contrast and relative measures for its primary endpoint. Presenting the group proportions alongside a risk difference helps readers distinguish the observed outcome frequencies from the estimated separation between groups. Confidence intervals add information about precision that a p-value alone cannot convey.

The registry also illustrates why design and analysis descriptions matter. A crossover model can create within-participant dependence, and the analysis may need to account for sequence and period. Yet the registry record does not report how the primary comparison was modeled. Readers can interpret the posted estimates, but cannot fully assess whether the analysis corresponds to the design using the available methods information.

Secondary outcomes add perspective on specimen adequacy and diagnosis after crossover, but they bring questions about multiplicity and participant selection. The registry's absence of reported analyses and a multiplicity plan makes it important to distinguish the primary endpoint from additional comparisons. Planning illustrations based on the observed effect also highlight how sample-size requirements depend on the effect researchers choose to detect; they are not the original trial justification.

These considerations make the record useful for statistical learning: effect measures, precision, crossover structure, secondary outcomes, and missing analysis details all influence interpretation. The trial's results are informative as posted, while the limitations in reporting constrain how far statistical conclusions can be extended.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations specific to this trial arise from the information recorded. The registry identifies a randomized crossover model but does not report the primary statistical analysis method. In particular, it does not explain whether the main comparison treated outcomes as paired, how sequence or period effects were addressed, or whether possible carryover was considered. These are important questions for a crossover design, but the record does not answer them.

The registry lists the conditions under study but does not provide participant characteristics or diagnostic-yield results by condition. The overall percentages may therefore combine different lesion types, and the record does not show whether results were similar across those groups. It also does not report detailed eligibility criteria or the setting and procedural details needed to assess how closely another population would match the trial participants.

The registry does not give an operational definition for a final diagnosis, explain who assessed diagnostic outcomes, or describe missing-data handling. Nor does it report the analysis populations or a full flow of participants through the trial and crossover. These gaps make it difficult to assess the effects of incomplete outcome information or departures from the intended procedures.

The secondary results are not accompanied by a reported multiplicity plan or analysis description. The adverse-event entries lack detailed definitions and collection methods, and death counts are not reported in the registry record. Finally, the trial's original sample-size justification and statistical plan are not reported. These limits concern what can be evaluated from the registry record; they do not establish that the underlying study did or did not address these issues elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prospective Trial of EUS-FNA Versus EUS-FNB Using a Novel Core Biopsy Needle — NCT01769248.
• Registry record last updated 2018-01-18; status last verified 2017-12.
• Results first posted 2015-03-18.
• 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

NCT01769248 is a completed randomized prospective crossover trial sponsored by Northwestern University, comparing EUS-FNA with EUS-FNB using a novel core biopsy needle. The registry lists enrollment of 140 and identifies diagnostic yield as the primary outcome, with a 1-year timeframe.

The posted primary results are 67.1% for aspiration and 90.0% for biopsy, with a risk difference of 0.229 and a 95% confidence interval from 0.098 to 0.359. The registry also reports outcomes for specimen adequacy and diagnosis after crossover. It lists zero serious and zero other adverse events in each group, while death counts are not reported in the registry record.

The registry does not report the original sample-size justification, detailed statistical plan, analysis populations, missing-data methods, or the primary model used for the crossover design. The estimates can be described as posted, but those omissions limit assessment of their analytic context and generalizability.