Evaluating Perioperative Dexamethasone and the Risk of Bleeding in Tonsillectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluating Perioperative Dexamethasone and the Risk of Bleeding in Tonsillectomy (NCT01415583), a randomized na study. The primary outcome is Number of Participants With Post-tonsillectomy Bleeding.

2. Clinical Question

The clinical question concerns a potential safety outcome in the period after surgery. The registry describes concern about bleeding and the use of perioperative steroids in tonsillectomy, and identifies post-operative hemorrhage as the condition under study. The comparison is between participants assigned to dexamethasone and participants assigned to saline, rather than a comparison of different steroid regimens.

The trial was prospective, randomized, and blinded according to its description. Random allocation is intended to make the comparison less vulnerable to systematic differences between groups at the outset; blinding is intended to limit the influence of treatment knowledge on care or assessment. These design features do not, on their own, establish that all potential sources of bias were prevented. Details about the success of masking and the outcome-assessment process are not reported in the registry record.

The primary question is framed around whether bleeding risk increases, but the registry does not include the noninferiority margin or a detailed protocol definition of the decision rule. Therefore, the posted counts and recalculated comparison can describe the observed data, while a complete assessment of the trial’s intended noninferiority claim requires information that is not reported in the registry record.

3. Trial Design

This was a completed, randomized, double-masked, parallel-group trial sponsored by Massachusetts Eye and Ear Infirmary. It enrolled 314 participants. The registry lists 157 participants in the saline arm and 157 in the dexamethasone arm. The study was classified as phase NA. Its recorded start was 2010-07, and its primary completion was 2011-11.

The study description characterizes the trial as prospective, randomized, blinded, and placebo-controlled. Saline was the placebo comparator, and dexamethasone was the active intervention. A parallel-group design assigns participants to one of the treatment groups and follows those groups during the specified outcome period; it does not mean participants crossed from one assignment to the other. The registry identifies double masking, but does not report which roles were masked or how masking was maintained.

The primary outcome was the number of participants with post-tonsillectomy bleeding, assessed over two weeks after surgery. The registry lists one outcome measure and two analysis entries. Both analysis entries identify the same groups and the same one-sided t-test method for noninferiority. The record does not provide the study protocol, dose details, eligibility criteria, recruitment setting, or the original sample-size justification.

Equal numbers are listed in the two arms, which is consistent with equal allocation in the posted results. That observation should not be treated as a full account of the randomization procedure: sequence generation, allocation concealment, and any stratification are not reported in the registry record. Nor does the completed status by itself indicate how many participants completed follow-up or were included in each analysis. Those analysis-population details are not reported.

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 Number of Participants With Post-tonsillectomy Bleeding, measured over 2 weeks after surgery.

The primary endpoint counts participants who experienced post-tonsillectomy bleeding during the two weeks after surgery. It is an event-count outcome at the participant level: a participant is counted as having the event rather than as contributing a continuous measurement. The registry labels the measure as the number of participants with post-tonsillectomy bleeding and gives participants as the unit.

Using a defined follow-up period helps specify which events belong to the primary outcome. A bleeding event after the stated period would not fall within that primary timeframe as described, although the registry does not provide additional details about event adjudication, severity categories, or how recurrent episodes were handled. Such definitions are not reported in the registry record.

For a safety question, the number of participants with an event can be compared between assigned groups. The registry reports 13 participants in the saline group and 17 in the dexamethasone group, with 157 participants listed in each arm. The posted comparison also includes a risk difference and an interval estimate. A risk difference expresses the difference between the groups’ event risks; it is not the same quantity as the raw difference in event counts when group sizes or denominators differ.

The outcome is relevant to the stated question because it directly records post-operative bleeding rather than an indirect marker. Its interpretation still depends on complete and consistent event ascertainment during follow-up. The registry record does not describe the method used to identify bleeding events or the handling of participants with incomplete follow-up.

7. Results Posted in the Registry

• Dexamethasone: 10.8% (17/157) versus 8.3% (13/157) on control; risk difference 2.5 percentage points (95% CI -3.9 to 9.0), risk ratio 1.31 (0.66–2.60); unadjusted two-proportion z-test p = 0.443.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either had post-tonsillectomy bleeding within the specified two-week period or did not. For a binary outcome, the event risk is the proportion of participants in a group who experience the event. The registry gives the event counts and arm sizes, and the recalculation compares the groups using a risk difference. In general, a risk difference is the event risk in one group minus the event risk in the comparison group. It is expressed on an absolute scale, so it describes the separation between risks rather than a relative change.

What does the risk difference convey?

The recalculated risk difference is positive, meaning the observed risk was higher in the dexamethasone arm than in the saline arm. The associated interval reaches across zero. In general, zero on a risk-difference scale represents equal risks; an interval spanning zero includes both no difference and values on either side. The interval therefore signals uncertainty about the direction and size of the underlying difference. It does not demonstrate that the groups are equivalent.

The posted unadjusted p-value is 0.443. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the probability that the findings are due to chance. A large p-value alone cannot establish no effect or rule out a meaningful difference. Interpretation requires the effect estimate, interval, outcome context, and analysis plan.

How does noninferiority differ from a conventional difference test?

In general, a noninferiority analysis asks whether the intervention is not worse than the comparator by more than a prespecified acceptable margin. This is not the same as asking whether the two groups have exactly equal outcomes. The margin is essential: it defines the largest difference that would still satisfy the intended noninferiority criterion. The registry lists one-sided t-tests and identifies the analyses as noninferiority analyses, but the noninferiority margin is not reported in the registry record. The reported entries also lack an estimate, interval, or test result that would permit the sponsor’s noninferiority conclusion to be assessed.

A one-sided test evaluates evidence in a specified direction, unlike a two-sided test that evaluates departures in either direction. In general, the choice of direction should be set in advance and should match the question and analysis plan. The record identifies a one-sided method and lists 0.05, but it does not clarify the complete decision rule or show the calculated statistic. No additional assumptions about the intended test should be inferred from that brief entry.

Why do the outcome type and model matter?

For event counts or risks, methods designed for binary data are commonly used to compare groups. A t-test is conventionally associated with comparing means of a quantitative outcome. The registry’s analysis entries state “t-test, 1 sided,” but do not specify what quantity was tested or provide a detailed statistical plan. It is therefore not possible to determine from the entry alone how that method was applied to this binary endpoint. This uncertainty is distinct from the straightforward unadjusted recalculation of the two reported group summaries.

General statistical methods depend on assumptions about the observations and the sampling process. For a binary endpoint, these include a suitable model for event probabilities and appropriate handling of dependence, missing outcomes, and the assignment design. The posted recalculation is unadjusted and does not incorporate covariates. The registry record does not report whether the sponsor’s analysis used adjustment, whether any clustering or stratification was present, or how missing outcomes were handled.

What can the registry analysis entries establish?

The entries establish that the registry records two analyses comparing saline and dexamethasone, both described as one-sided t-tests for noninferiority. They do not provide a numerical effect, interval, or outcome-specific result. The entries also do not identify a noninferiority margin, define an analysis population, or describe treatment of protocol deviations. Those missing details limit assessment of the sponsor’s statistical method and prevent reconstruction of its decision from the registry record.

The recalculation uses the posted group summaries and is explicitly unadjusted. It can be read as a transparent descriptive comparison of the observed risks, not as a replacement for the trial’s prespecified analysis. No discrepancy is flagged between the recalculation and a sponsor estimate, but the registry does not present a sponsor estimate with which to make a detailed numerical comparison. The primary methodological interpretation should therefore keep the two kinds of information distinct: the reported design label and test method, and the available descriptive statistics and unadjusted comparison.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The registry gives arm-level outcome estimates with 97.5% confidence intervals, and the recalculated comparison has an interval around the risk difference. The confidence level for that comparison interval is not specified in the registry record. A confidence interval is a range produced by a statistical procedure; in general, narrower intervals indicate greater precision under the method’s assumptions, while wider intervals indicate greater uncertainty.

The risk-difference interval extends across zero. This means the posted data are compatible with no difference as well as with effects in either direction within the interval. The point estimate is positive, but the interval indicates that its direction and magnitude are not determined precisely. The unadjusted p-value of 0.443 is consistent with the lack of a clear separation from zero in this comparison, but a p-value is not a substitute for the interval or a direct measure of precision.

There are 157 participants listed in each group, with 13 and 17 recorded events. The observed event counts are limited, and estimates based on binary events can remain uncertain even when the groups are the same size. The registry’s arm-level intervals are labeled 97.5%; the comparison interval should not be assumed to have the same confidence level because its level is not specified.

Precision is also distinct from bias and validity. A narrow interval would not correct systematic errors in outcome ascertainment, missing data, or an unsuitable analysis. Conversely, an imprecise estimate can still accurately reflect uncertainty in the available observations. The registry record does not report enough detail about follow-up completeness, event assessment, or analysis populations to assess those issues fully.

11. 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 are participants per arm, not total events. They are illustrations based on the observed effect, rather than the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is set to the stated fraction of the observed effect.

Planning for 100% of the observed effect gives 2,089 participants per arm for 80% power and 2,796 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,603 participants per arm for 80% power and 4,823 participants per arm for 90% power. Planning for 50% of the observed effect gives 7,856 participants per arm for 80% power and 10,516 participants per arm for 90% power.

In general, power is the probability that a study will meet its defined statistical criterion when a specified effect is present, under the planning assumptions. The 80% column represents the participant count per arm used for a design targeting 80% power; the 90% column represents the count per arm for a design targeting 90% power. These percentages describe design targets, not probabilities that the observed trial result is correct. Smaller effects require more participants to distinguish them from random variation, which is why the planning counts rise as the assumed fraction of the observed effect falls.

These figures are planning illustrations, not observed power. The registry record does not report the original sample-size justification or establish that the trial was designed around these assumptions. The displayed projections rely on the observed effect, which is itself uncertain, so they should not be read as evidence that a future study will achieve the stated power unless the assumptions and analysis plan are appropriate.

12. 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 = 0.083; treatment proportion p₁ = 0.108; average p̄ = 0.096.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4157 = 0.8148.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4153 = 0.3496.
4. n = (0.8148 + 0.3496)² / (0.0255)² = 2,088.6, rounded up to 2,089 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 <- 0.0828025477707006                          # control proportion
p1 <- 0.10828025477707                          # 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(1415583)
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 = 2,089 (80% power), 2,796 (90% power)
 75% of observed effect: n per arm = 3,603 (80% power), 4,823 (90% power)
 50% of observed effect: n per arm = 7,856 (80% power), 10,516 (90% power)
power.prop.test: 2088.6 
Simulated power at n = 2,089 per arm: 0.797 (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.

13. Analyses Reported by the Sponsor

The registry’s sponsor-analysis entries identify two analyses of the saline and dexamethasone groups. Each is described as a one-sided t-test for noninferiority, and each lists 0.05. Neither entry gives an outcome estimate, confidence interval, or calculated test result. The noninferiority margin and the analysis population are also not reported in the registry record.

The recalculation is a simple unadjusted comparison of the posted event summaries. It reports a positive risk difference, an interval spanning zero, and an unadjusted p-value of 0.443. Those quantities describe a risk-based comparison and should not be presented as if they were the missing result of the registry’s t-test. The available record does not specify enough detail to establish that the two analyses used the same estimand, assumptions, or decision rule.

No discrepancy is flagged between the recalculation and a sponsor estimate. However, because no numerical sponsor estimate or test result is posted, that absence does not amount to an independent numerical confirmation of the sponsor’s analysis. The sponsor’s original analysis plan and detailed results are not reported in the registry record, so the relationship between the analysis methods cannot be fully evaluated.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and two analysis entries. Both entries concern the same two groups and are described as one-sided t-tests for noninferiority. The record does not explain why there are two entries or whether they represent distinct populations, endpoints, or analysis versions. No secondary outcome measures are posted.

Multiplicity arises when a study conducts multiple statistical tests or makes multiple outcome-based claims. In general, testing many outcomes or comparisons can increase the chance of at least one apparently unusual result, so a prespecified strategy may define a primary test or adjust interpretation. The registry record does not report a multiplicity-adjustment plan, and the available information is not enough to determine whether adjustment was necessary for the sponsor’s complete analysis.

The registry identifies the primary outcome as bleeding during the two weeks after surgery, but does not provide a protocol-defined outcome hierarchy beyond that. It also does not state whether there were interim analyses, repeated looks at accruing data, or other planned comparisons. Those details are not reported in the registry record and should not be inferred from the two analysis entries.

Missing-data methods are not reported. The record does not state how participants with incomplete follow-up were handled, whether outcomes were imputed, or whether analyses used a complete-case approach. Although 157 participants are listed in each arm, the listed group sizes do not establish that all randomized participants had complete outcome information or were included in every analysis.

The analysis-population definitions are likewise not reported. The registry does not say whether the sponsor used all randomized participants, participants treated as assigned, participants who received the assigned intervention, or a protocol-compliant subset. In general, noninferiority analyses can be sensitive to population choices and deviations from assigned treatment, so these details matter to interpretation. Without the definitions, the sponsor analysis cannot be fully assessed or reproduced from the registry record.

The noninferiority margin, analysis plan, and protocol are not reported. These omissions leave uncertainty about the intended decision rule and how the two analysis entries relate to it. They do not alter the observed counts, but they limit the conclusions that can be drawn about the planned inferential claim.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The adverse-event record lists 157 participants at risk in each group. In the saline group, it records zero serious adverse events, zero other adverse events, and zero deaths. In the dexamethasone group, it also records zero serious adverse events, zero other adverse events, and zero deaths. No serious adverse-event terms are listed.

These figures describe what the registry reports for the specified safety categories. They should not be expanded into a claim that no adverse events of any kind occurred, because the record distinguishes serious from other adverse events and gives zero in both categories as posted. The registry does not provide further event definitions, ascertainment methods, or a detailed account of follow-up for safety outcomes.

Zero recorded events in both groups means there is no between-group contrast to estimate from these entries for those listed categories. It does not establish that the groups have identical safety profiles or that rare events are excluded. In general, the absence of observed events in a study of limited size can coexist with uncertainty about the frequency of uncommon outcomes.

The primary outcome of post-tonsillectomy bleeding is reported separately from these adverse-event summaries. The safety figures should therefore be read as their own registry entries, not as a replacement for the primary bleeding outcome or a complete description of all possible harms.

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

The posted results show bleeding events in both groups: 13 participants in the saline group and 17 in the dexamethasone group, with 157 participants listed in each arm. The unadjusted risk-difference estimate points toward a higher observed risk in the dexamethasone group, but its interval crosses zero and the unadjusted p-value is 0.443. The estimate is therefore uncertain; the data do not precisely establish the direction or size of a difference.

These results do not establish that the treatments are equivalent. Failure to show a statistically clear difference is not the same as showing that any difference is negligible. Nor do the posted recalculated statistics, by themselves, rule out an increase in bleeding. An interval that spans zero can include both no difference and nonzero differences, and the record does not report the noninferiority margin needed to assess a noninferiority claim.

The registry’s sponsor-analysis entries label the method as a one-sided t-test for noninferiority but do not include a numerical estimate or test result. Without the margin, detailed analysis plan, and analysis population, the sponsor’s intended noninferiority conclusion cannot be reconstructed from those entries. The unadjusted recalculation provides a separate, transparent description of the posted group summaries, not a replacement for the missing details of the planned analysis.

The safety entries list zero serious adverse events, zero other adverse events, and zero deaths in each group. These are the recorded figures, not proof that all possible harms have been excluded. Further information about safety outcome collection is not reported in the registry record.

The appropriate statistical reading is limited to the available evidence: observed bleeding counts, an uncertain unadjusted comparison, and sparse detail about the sponsor’s inferential analysis. These findings do not, on their own, support a broad claim about whether dexamethasone does or does not cause bleeding. That interpretation would require the protocol, complete analysis results, and information about outcome ascertainment and missing data, none of which is reported in the registry record.

17. Why This Trial Matters Statistically

This trial addresses a clearly defined statistical challenge: comparing the frequency of a post-operative safety event between randomized groups. The endpoint is binary, the assigned groups are balanced in the posted counts, and the event period is specified as two weeks after surgery. These features make the observed comparison understandable, while the uncertainty around the effect remains important to interpretation.

The trial also illustrates why a noninferiority label is not enough to interpret a result. A noninferiority analysis depends on a margin chosen before examining the outcome and on a decision rule that compares the estimated effect and its uncertainty with that margin. The registry identifies noninferiority analyses but does not report the margin or the numerical sponsor result. Readers therefore cannot verify the stated inferential objective from the registry entries alone.

The contrast between the observed counts and the uncertainty is another useful statistical lesson. The dexamethasone group has more recorded events, but the recalculated interval includes zero. The direction of the point estimate is not a definitive finding about the underlying risks. Estimates need to be read with their precision rather than as isolated counts or as a yes-or-no result based only on a p-value.

Finally, the planning illustrations show how sample-size needs depend on the effect targeted: smaller assumed effects require larger planned groups. They do not establish the trial’s original design rationale, which is not reported. The combination of a completed randomized study, an interpretable event count, and important gaps in the posted analysis details makes this record useful for distinguishing what the data describe from what the registry does not allow readers to conclude.

18. Limitations

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

The registry record leaves several trial-specific details unavailable. It does not report the dose, route, or precise timing of dexamethasone, nor does it describe the saline administration in detail. Eligibility criteria, recruitment setting, participant ages, and baseline characteristics are not reported. Although the study summary discusses children undergoing tonsillectomy, the enrolled population’s age composition is not specified in the record.

The bleeding endpoint is described by its name and two-week timeframe, but the record does not define the event in operational detail. It does not explain how bleeding was identified, whether events were independently adjudicated, how severity was classified, or how repeated events for one participant were counted. These details affect interpretation of a participant-level event outcome.

The registry does not report outcome completeness or the handling of missing follow-up. It lists 157 participants in each arm, but does not establish whether all randomized participants were assessed for the primary outcome or included in each analysis. Analysis populations and protocol deviations are not described.

Important elements of the noninferiority plan are also absent: the margin, original sample-size justification, and detailed statistical analysis plan are not reported. The listed sponsor analyses do not include an effect estimate, confidence interval, or test result. The registry also does not report whether interim analyses or multiplicity adjustments were planned. As a result, the sponsor’s inferential decision cannot be fully evaluated from the posted analysis entries.

These gaps do not change the counts recorded in the results, but they constrain how far those results can be interpreted. In particular, the unadjusted recalculation cannot substitute for unreported protocol definitions, analysis populations, or sponsor methods.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluating Perioperative Dexamethasone and the Risk of Bleeding in Tonsillectomy — NCT01415583.
• Registry record last updated 2017-07-12; status last verified 2017-06.
• Results first posted 2017-07-12.
• 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

NCT01415583 is a completed randomized, double-masked, parallel-group trial sponsored by Massachusetts Eye and Ear Infirmary. It enrolled 314 participants, with 157 listed in the saline group and 157 in the dexamethasone group. The primary outcome was the number of participants with post-tonsillectomy bleeding during the two weeks after surgery.

The registry reports 13 bleeding events in the saline group and 17 in the dexamethasone group. An unadjusted recalculation gives a positive risk-difference estimate, an interval spanning zero, and a p-value of 0.443. The registry also lists one-sided t-tests for noninferiority, but does not provide the numerical sponsor results or noninferiority margin.

The adverse-event entries list zero serious adverse events, zero other adverse events, and zero deaths in both groups. Missing-data procedures, analysis populations, and the original sample-size justification are not reported in the registry record.