A Dose Ranging Placebo-Controlled Double-Blind Study to Evaluate the Safety and Efficacy of Tezepelumab in Atopic Dermatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Dose Ranging Placebo-Controlled Double-Blind Study to Evaluate the Safety and Efficacy of Tezepelumab in Atopic Dermatitis (NCT03809663), a randomized phase 2 study. The primary outcome is Number of Participants With Investigator's Global Assessment (IGA) Score of 0 (Clear) or 1 (Almost Clear) (IGA 0/1) at Week 16.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-group phase 2 study sponsored by Amgen. The registry record lists atopic dermatitis as the condition and an enrollment of 251 participants. The study began on 2019-03-15, had a primary completion date of 2020-05-12, and is listed as terminated. The reason for termination is not reported in the registry record.

The official title describes a dose-ranging study of tezepelumab alone or combined with topical corticosteroids in moderate-to-severe atopic dermatitis. Part A included placebo and three tezepelumab dose schedules: 210 mg Q4W, 280 mg Q2W, and 420 mg Q2W. The arm descriptions specify treatment for a maximum of 52 weeks. The 210 mg and 280 mg regimens included an initial 420 mg dose, followed by the assigned schedule; the 210 mg group received placebo at Week 2 to maintain masking. The placebo description also includes switching non-responders to tezepelumab after Week 16.

Part B is described as comparing placebo plus topical corticosteroids with tezepelumab 420 mg Q2W plus topical corticosteroids. The primary endpoint results posted for this analysis are the Part A comparisons at Week 16. The registry record does not report the original sample-size justification, the planned allocation ratio, or the reason for termination. It also does not give enough detail to reconstruct how participants were assigned between the two study parts.

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: Enrollment of Part A of this study was completed as of 27 July 2020. The study was terminated prior to the enrollment of any participants into Part B.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS: All randomized participants.

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.

Population: Full analysis set (FAS): All randomized participants in Part A.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Investigator's Global Assessment (IGA) Score of 0 (Clear) or 1 (Almost Clear) (IGA 0/1) at Week 16, measured over Week 16.

The primary endpoint is the number of participants with an Investigator’s Global Assessment (IGA) score of 0 or 1 at Week 16. The IGA is a clinician’s assessment of overall atopic dermatitis severity at a single time point. Its scale runs from 0, clear, through 5, very severe. The assessment uses erythema, infiltration, papulation, oozing, and crusting as clinical characteristics. A score of 0 or 1 represents the endpoint’s specified response category; it does not capture every dimension of the condition or its course.

Counting participants in a defined response category makes the primary outcome binary: each participant is either counted as a responder or not counted as a responder under the registry’s definition. This can make between-group response proportions straightforward to describe. The endpoint is anchored at Week 16, so it does not by itself describe when a response began, whether it persisted, or later outcomes.

The registry record specifies that participants who took rescue medication between Day 29 and Week 16 were treated as non-responders. That rule is part of the endpoint definition and affects how the observed counts should be interpreted. The analysis population is identified as the FAS, meaning all randomized participants. The record does not provide further details in the endpoint description about how other missing Week 16 assessments were handled.

7. Results Posted in the Registry

• Part A: Tezepelumab 210 mg Q4W: 6.5% (4/62) versus 3.2% (2/63) on control; risk difference 3.3 percentage points (95% CI -4.2 to 10.8), risk ratio 2.03 (0.39–10.70); unadjusted two-proportion z-test p = 0.391.
• Part A: Tezepelumab 280 mg Q2W: 3.2% (2/63) versus 3.2% (2/63) on control; risk difference 0.0 percentage points (95% CI -6.1 to 6.1), risk ratio 1.00 (0.15–6.88); unadjusted two-proportion z-test p = 1.000.
• Part A: Tezepelumab 420 mg Q2W: 7.9% (5/63) versus 3.2% (2/63) on control; risk difference 4.8 percentage points (95% CI -3.2 to 12.7), risk ratio 2.50 (0.50–12.41); unadjusted two-proportion z-test p = 0.243.

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.

Change From Baseline in Scoring of Atopic Dermatitis (SCORAD) at Week 16

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Part A: Tezepelumab 210 mg Q4W: mean -16.75 versus -8.00 on control; difference -8.75 (95% CI -15.61 to -1.89), standardized effect d = -0.45; z-test p = 0.012.
  • Part A: Tezepelumab 280 mg Q2W: mean -11.87 versus -8.00 on control; difference -3.87 (95% CI -10.86 to 3.12), standardized effect d = -0.19; z-test p = 0.278.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Part A: Tezepelumab 210 mg Q4W than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part A: Tezepelumab 280 mg Q2W and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Pruritus Numeric Rating Scale (NRS) at Week 16

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Part A: Tezepelumab 210 mg Q4W: mean -1.40 versus -0.71 on control; difference -0.69 (95% CI -1.48 to 0.10), standardized effect d = -0.31; z-test p = 0.087.
  • Part A: Tezepelumab 280 mg Q2W: mean -0.94 versus -0.71 on control; difference -0.23 (95% CI -1.03 to 0.57), standardized effect d = -0.10; z-test p = 0.575.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part A: Tezepelumab 210 mg Q4W and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part A: Tezepelumab 280 mg Q2W and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints cover several dimensions: EASI response thresholds and time to those thresholds, SCORAD, pruritus NRS, and serum trough concentrations. The numeric summaries discussed in the posted results include SCORAD and pruritus NRS changes from baseline at Week 16. Their group patterns are not uniform across outcomes or dose groups, and the uncertainty around the recalculated comparisons varies. Taken together, they do not create a single consistent statistical picture that resolves the uncertainty in the primary IGA endpoint.

Secondary outcomes can add context because they measure aspects of disease severity, symptoms, response timing, or drug exposure that the primary endpoint does not capture. They remain distinct outcomes, however, and they do not substitute for the primary endpoint. A difference on a continuous scale is not directly interchangeable with the proportion meeting the IGA response definition.

The secondary comparisons are unadjusted, and the registry record does not report a multiplicity plan or hierarchy for interpreting them. When multiple outcomes and comparisons are examined, some may appear notable by chance even when there is no corresponding underlying effect. This is a general statistical concern, not evidence that any particular result is spurious. The unadjusted secondary results should be treated as exploratory signals requiring cautious interpretation, rather than as independent confirmation of the primary result.

The registry record lists six posted secondary outcomes and eight outcome measures overall. It does not provide numeric results for every secondary outcome in the summaries. Consequently, the overall secondary pattern can only be characterized at the level of the listed outcomes and the numeric summaries that are posted, not as a complete assessment of every secondary measure.

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

• Number of Participants Who Experienced a 50% or 90% Reduction From Baseline in Eczema Area and Severity Index (EASI 50/90) at Week 16
• Time to Achievement of 50%, 75% or 90% Reduction From Day 1 in Eczema Area and Severity Index (EASI 50/75/90)
• Change From Baseline in Scoring of Atopic Dermatitis (SCORAD) at Week 16
• Change From Baseline in Pruritus Numeric Rating Scale (NRS) at Week 16
• Serum Trough Concentrations of Tezepelumab After Q2W or Q4W Administration
• Serum Trough Concentrations of Tezepelumab After Switching to 420 mg Q2W Administration After Week 16

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, the posted counts give the number of participants meeting the IGA 0/1 definition in each Part A group. The recalculated comparisons express the contrast as an unadjusted risk difference, meaning the response proportion in the tezepelumab group minus the response proportion in placebo. A value of zero denotes no difference on that scale. The estimates and confidence intervals are simple unadjusted recalculations from the posted summary statistics; the registry also reports sponsor analyses using logistic regression.

What does a confidence interval describe?

In general, a confidence interval is a range of values compatible with the observed data under the method used to construct it. It communicates uncertainty around an estimate, rather than giving a probability that the true effect lies in the particular interval. For a risk difference, zero represents no difference; for an odds ratio, one represents no difference. An interval that includes the corresponding no-difference value does not prove there is no effect. It indicates that the data and analysis do not distinguish the estimate from that value at the interval’s stated confidence level.

Why are the primary estimates uncertain?

The response counts are low in all four groups. With few observed events, each participant’s outcome can have a substantial influence on a group’s response proportion. This makes the estimates sensitive to small changes in the observed counts and contributes to wide uncertainty intervals. The risk-difference intervals span values below and above zero, and the sponsor’s odds-ratio intervals span values below and above one. The two scales are not interchangeable, so their numerical estimates should not be compared as if they measured the same quantity.

What is the role of the sponsor’s model?

The registry reports logistic regression for the primary comparisons, with odds ratios, 95% confidence intervals, and p-values. Logistic regression models the odds of the binary response. The registry record does not report the full model specification, including whether covariates were included or what other modeling choices were made. The recalculated risk differences are unadjusted summaries based directly on the posted group counts. They are useful for describing absolute differences on the response-proportion scale, but they are not a replacement for the sponsor’s reported model analysis.

How should the secondary summaries be read?

The posted numeric summaries include changes from baseline in SCORAD and the Pruritus Numeric Rating Scale at Week 16. These are continuous outcomes, reported as least-squares means with standard errors. The recalculated group comparisons use mean differences. A negative change represents a decrease from baseline as recorded on the scale; interpretation of the clinical meaning of a change depends on the scale and context, which are not fully described in the registry record.

The recalculated standard deviations for these comparisons are identified as approximate, because they were inferred from the reported standard errors. The resulting standardized effect summaries and planning illustrations therefore inherit that approximation. General statistical practice treats a mean difference and its uncertainty as summaries of a group contrast; standardizing that difference can help express its size relative to variability, but it does not make distinct clinical scales equivalent.

The secondary comparisons are unadjusted. A collection of separate tests creates a multiplicity concern: when many hypotheses are examined, the chance of at least one apparently notable result can increase. The registry record does not report a multiplicity adjustment or a prespecified hierarchy among these endpoints. The individual unadjusted p-values should consequently be considered exploratory rather than as a set of confirmatory claims.

What analysis details are missing?

The primary population is identified as all randomized participants, and the rescue-medication rule is stated. However, missing-data procedures beyond that rule are not reported in the registry record. The record does not report the original sample-size justification, interim-analysis plans, or a complete statistical analysis plan. It also does not state how the primary and secondary hypotheses were ordered or whether any additional analyses were prespecified. These omissions limit the ability to assess design assumptions and the complete inferential strategy.

General statistical interpretation depends on aligning the endpoint definition, population, estimator, and uncertainty measure. For this trial, the IGA endpoint is binary, the sponsor’s reported method is logistic regression, and the posted recalculation is an unadjusted risk difference. Reading those approaches together gives both a model-based relative measure and an absolute difference, while keeping their assumptions and scales distinct.

11. Confidence Intervals and Precision

The primary endpoint estimates are imprecise. For 210 mg Q4W, the recalculated risk difference is 0.033, with a 95% confidence interval from -0.042 to 0.108. For 280 mg Q2W, it is 0.0, with an interval from -0.061 to 0.061. For 420 mg Q2W, it is 0.048, with an interval from -0.032 to 0.127. Every interval includes zero and allows a range of plausible differences in both directions.

The sponsor’s odds-ratio intervals are also broad: 0.290 to 9.809, 0.135 to 7.551, and 0.390 to 11.800 for the three dose groups, respectively. Each includes one, the no-difference value for an odds ratio. The width of these intervals is consistent with the limited information in groups with only a small number of observed responses. It means the estimates do not pin down the size or direction of a possible difference precisely.

In general, a confidence interval communicates the range of estimates that remain compatible with the data and analysis method; it is not a guarantee that the true effect is inside the interval. Precision is distinct from whether a p-value crosses a conventional threshold. A non-small p-value does not demonstrate equivalence, and an interval spanning the no-difference value does not prove the absence of a treatment effect.

The registry record gives sponsor confidence intervals for the logistic-regression odds ratios and the recalculated intervals for risk differences. Because the effect measures differ, the intervals should be interpreted on their own scales rather than directly compared numerically. The main statistical point is that neither set of intervals provides a narrow estimate of the Week 16 contrast.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations translate an observed effect into hypothetical planning requirements; they are not the trial’s original design calculations. For these binary primary comparisons, the figures are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future comparison to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column describes the corresponding requirement for a 90% chance. These are planning probabilities under a model, not guarantees about what a future study will find. The displayed quantities are not observed power.

The rows based on 100%, 75%, and 50% of the observed effect illustrate how the required sample changes when the target effect is made smaller. Smaller effects need more participants, because they are harder to distinguish from sampling variation. The observed primary effects are based on very few response events, so planning directly from them can produce unstable estimates of the effect a future trial should target. The sample-size figures should therefore be read as conditional illustrations, not as evidence that the trial was adequately or inadequately sized under its original design.

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 = 0.032; treatment proportion p₁ = 0.065; average p̄ = 0.048.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3027 = 0.5933.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3018 = 0.2540.
4. n = (0.5933 + 0.2540)² / (0.0328)² = 668.5, rounded up to 669 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 <- 0.0317460317460317                          # control proportion
p1 <- 0.0645161290322581                          # 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(3809663)
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 = 669 (80% power), 895 (90% power)
 75% of observed effect: n per arm = 1,093 (80% power), 1,463 (90% power)
 50% of observed effect: n per arm = 2,241 (80% power), 3,000 (90% power)
power.prop.test: 668.5 
Simulated power at n = 669 per arm: 0.804 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons from logistic regression. The odds ratio for 210 mg Q4W versus placebo is 1.686, with a 95% confidence interval of 0.290 to 9.809 and p = 0.56. For 280 mg Q2W, the odds ratio is 1.011, with a 95% confidence interval of 0.135 to 7.551 and p = 0.99. For 420 mg Q2W, the odds ratio is 2.146, with a 95% confidence interval of 0.390 to 11.800 and p = 0.38.

The recalculated unadjusted risk differences are 0.033, 0.0, and 0.048 for those same comparisons, with p-values of 0.391, 1.0, and 0.243. These are different estimators on different scales: the odds ratios come from the sponsor’s logistic-regression analyses, while the risk differences are recalculated directly from the posted counts. Their numerical values should not be treated as directly comparable.

The registry record does not give the full logistic model specification, so the reason for the differences between the reported odds ratios and the simple unadjusted calculations cannot be determined from the record. Both sets of results have substantial uncertainty and do not provide a precise estimate of the Week 16 contrast. The record’s discrepancy indicator is false.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis considers several hypotheses, endpoints, doses, or time points. In general, conducting many tests without adjustment increases the chance of obtaining at least one apparently unusual result by chance. Methods such as a prespecified testing hierarchy or an adjustment to the significance threshold can address that issue, but the appropriate approach depends on the trial’s aims and design.

The registry record reports three sponsor logistic-regression comparisons for the primary endpoint and multiple secondary outcomes. It does not report whether the primary dose comparisons were adjusted for multiplicity, whether a testing sequence was used, or whether the secondary outcomes were subject to a formal hierarchy. The posted secondary comparisons are unadjusted. Without a reported plan, the strength of evidence across the collection of results cannot be evaluated as if each p-value were an isolated confirmatory test.

The primary population is described as the FAS, defined as all randomized participants. The endpoint description also specifies that participants who used rescue medication from Day 29 through Week 16 were considered non-responders. That provides one rule for interpreting the endpoint, but it does not explain how other missing or unevaluable Week 16 assessments were treated. Missing-data methods are not reported in the registry record.

The record does not report an interim-analysis plan, the original sample-size justification, or a complete statistical analysis plan. It therefore does not establish whether any interim monitoring or other planned inferential procedures were used. These absences should not be filled in by assumption. They limit the ability to assess how the reported analyses relate to the study’s original design and what safeguards, if any, were planned for repeated testing or incomplete outcome data.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: alcohol abuse (5.3%), ascites (5.0%), hepatic cirrhosis (5.0%), cellulitis (5.0%), device failure (5.0%).

The registry lists serious adverse events by treatment group and by later treatment sequences, with the number at risk and the number affected. Among the four initial Part A groups, the listed serious-event counts are 0 of 63 for placebo, 2 of 59 for tezepelumab 210 mg Q4W, 0 of 58 for tezepelumab 280 mg Q2W, and 1 of 70 for tezepelumab 420 mg Q2W. No deaths are listed in any of the reported groups.

The at-risk counts in the safety listings differ from the primary endpoint analysis denominators. The registry also lists groups with treatment sequences that include continued treatment or switching from placebo to tezepelumab. Those groups should be read as the registry labels them, rather than combined into a single comparison without additional information. Follow-up duration and exposure-adjusted safety measures are not reported in the listed summary, so the counts alone do not establish comparative rates over equivalent exposure.

The serious-event counts are descriptive and do not establish that a treatment caused or prevented an event. The registry lists several serious-event terms with percentages, but the denominator and method for those percentages are not reported in the registry record. Caution is therefore needed in interpreting those term-level figures.

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

The primary result is a comparison of the number of participants meeting a specified IGA response definition at Week 16. The posted counts are small, and both the sponsor’s odds-ratio intervals and the recalculated risk-difference intervals are broad. The results therefore give an uncertain estimate of the contrasts between the Part A dose groups and placebo. The direction and size of any underlying difference are not determined precisely by these data.

These results do not establish equivalence between tezepelumab and placebo, nor do they establish a benefit or lack of benefit. A comparison whose interval includes the no-difference value can remain compatible with effects in either direction. The p-values should not be read as the probability that a treatment effect exists, or as a measure of its clinical importance.

The endpoint is one clinician-assessed response category at one time point, with rescue medication use counted as non-response. It does not by itself describe symptom experience, all disease features, durability of response, or outcomes after Week 16. The registry contains other endpoints, but each addresses a distinct question and carries its own measurement and multiplicity limitations.

The study is listed as terminated, and the reason is not reported in the registry record. The record also does not report the original sample-size rationale or complete analysis plan. Those gaps limit context for assessing why the study ended and how its analyses were intended to support inference. The most defensible reading is that the posted Week 16 data yield imprecise comparisons, not a definitive conclusion about the treatment effect.

18. Why This Trial Matters Statistically

This trial illustrates why effect estimates and uncertainty need to be read together. The response counts are low, and the unadjusted risk differences differ across the dose groups. Looking only at the point estimates could suggest a pattern, but the confidence intervals show that the estimates are compatible with a wide range of contrasts. The sponsor’s logistic-regression intervals likewise show substantial uncertainty on the odds-ratio scale.

It also demonstrates how analysis choices affect the form of a result. A risk difference expresses an absolute contrast in response proportions, whereas an odds ratio expresses a relative contrast in odds. They answer related but distinct statistical questions. Presenting the sponsor’s model-based results alongside transparent unadjusted recalculations helps distinguish the registry’s reported analysis from a direct summary of the observed counts.

The secondary outcomes raise a further issue: many endpoints, doses, and time points can produce a collection of p-values that is difficult to interpret without a stated multiplicity strategy. The registry record does not report such a strategy. A statistically notable secondary comparison should therefore not automatically be treated as confirmation of the primary endpoint.

Finally, the record identifies the analysis population and rescue-medication rule, but not all missing-data, sample-size, or modeling details. Recognizing those omissions is part of statistical interpretation. The trial is informative about what was observed and how uncertain the comparisons are, while leaving important design and analysis questions unresolved.

19. Limitations

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

The primary endpoint results are based on few observed responses in each group, which limits precision. The confidence intervals are broad, and the posted results do not tightly determine the direction or size of the treatment contrasts. These findings are specific to the Week 16 IGA 0/1 outcome and should not be generalized automatically to other clinical measures or time points.

The registry record does not report the reason the study was terminated. It also does not report the original sample-size justification, the full statistical analysis plan, the complete logistic-regression model specification, or how missing Week 16 values other than rescue-medication cases were handled. Those omissions make it difficult to assess the full design rationale and the assumptions behind the sponsor’s analyses.

The primary sponsor comparisons are reported as logistic-regression odds ratios, while the recalculated comparisons are unadjusted risk differences. Since the full model details are unavailable, the two approaches cannot be reconciled beyond noting that they use different effect measures and methods. The secondary summaries are also unadjusted, and no multiplicity strategy is reported.

Safety listings include different at-risk counts across treatment groups and later treatment sequences. The registry summary does not provide the follow-up time or exposure-adjusted rates needed to make a like-for-like safety comparison. The secondary endpoint list is broader than the numeric summaries discussed in the record, so a complete synthesis of every listed secondary outcome is not possible from the posted numeric results alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Dose Ranging Placebo-Controlled Double-Blind Study to Evaluate the Safety and Efficacy of Tezepelumab in Atopic Dermatitis — NCT03809663.
• Registry record last updated 2022-03-10; status last verified 2022-03.
• Results first posted 2022-03-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03809663 is a randomized, quadruple-masked, parallel-group phase 2 study sponsored by Amgen, evaluating tezepelumab in moderate-to-severe atopic dermatitis. The registry lists an enrollment of 251 and a terminated status. The primary endpoint is the number of participants with an IGA score of 0 or 1 at Week 16, with rescue-medication use from Day 29 to Week 16 counted as non-response.

In Part A, the posted primary counts were 2 of 63 for placebo, 4 of 62 for tezepelumab 210 mg Q4W, 2 of 63 for 280 mg Q2W, and 5 of 63 for 420 mg Q2W. The sponsor’s logistic-regression comparisons and the unadjusted recalculations are imprecise. The registry also describes a Part B topical-corticosteroid regimen and lists secondary outcomes and safety data. The reason for termination and several design and analysis details are not reported in the registry record.