A Phase 2a, Randomized, Placebo Controlled, Study to Evaluate the Safety and Efficacy of AMG 557/MEDI5872 in Primary Sjögren's Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 2a, Randomized, Placebo Controlled, Study to Evaluate the Safety and Efficacy of AMG 557/MEDI5872 in Primary Sjögren's Syndrome (NCT02334306), a randomized phase 2 study. The primary outcome is Change From Baseline in European League Against Rheumatism Sjogren's Syndrome Disease Activity Index (ESSDAI) Score at Day 99.

2. Clinical Question

The central statistical question is whether the estimated group contrast is sufficiently clear and precise to distinguish it from no difference, while also considering the small analyzed groups and the range of effects compatible with the confidence interval. The registry record does not report a threshold for a clinically important difference, so the magnitude cannot be classified against such a threshold using these data alone.

3. Trial Design

This was a randomized, triple-masked, parallel-group Phase 2a study with placebo control. The registry lists MedImmune LLC as sponsor and records the study as completed. Enrollment was 32 participants. The study evaluated the safety and efficacy of AMG 557/MEDI5872 in primary Sjögren's syndrome; the intervention arm descriptions identify MEDI5872 210 mg and matching placebo.

During the double-blind period, the MEDI5872 group was scheduled to receive 210 mg subcutaneously every week from Days 1 to 15 and then every two weeks from Days 29 to 85. The placebo group was scheduled to receive matching placebo on the corresponding schedule. The record describes an open-label period after the blinded phase, during which participants initially assigned to placebo received MEDI5872. Consequently, safety summaries organized by any MEDI5872 exposure are not interchangeable with comparisons by original randomized assignment.

The primary outcome was change from baseline to Day 99 in ESSDAI score. The primary outcome description identifies baseline as Day 1 predose and specifies that adjusted mean change and standard error were presented. It defines the analysis population as randomized and treated participants grouped according to assigned treatment, with the outcome-specific analyzed number indicating how many participants were evaluated.

The original design’s sample-size justification, planned power, and assumptions are not reported in the registry record. The record also does not report the planned statistical analysis protocol in enough detail to establish the full prespecified model or analysis procedures. The posted ANCOVA result identifies the analysis method used for the primary comparison, but it does not by itself establish every feature of the original plan.

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: A total of 59 participants were screened in the study. Of which, 27 participants were screen failures and 32 participants were randomized and enrolled in study. The results are posted per the data of primary efficacy analysis last participant last visit date.

Double-blind Period

Reasons for not completing this period:

Open-label Period

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all randomized and treated participants, grouped according to assigned treatment. The "Overall Number of Participants Analyzed" denotes the number of participants evaluated for this outcome measure.

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 Change From Baseline in European League Against Rheumatism Sjogren's Syndrome Disease Activity Index (ESSDAI) Score at Day 99, measured over Baseline (Day 1 predose) and Day 99.

The primary endpoint is change from baseline in ESSDAI score at Day 99. ESSDAI is a physician-assessed index of Sjögren's syndrome disease activity. It covers 12 organ-specific domains: constitutional, lymphadenopathy, articular, muscular, cutaneous, glandular, pulmonary, renal, peripheral nervous system, central nervous system, hematological, and biological. Each domain is assessed at activity levels ranging from no activity through low, moderate, or high activity. Domain scores are weighted, and the overall score is the sum of the weighted domain scores. The scale ranges from 0, representing best, to 123, representing worst activity; higher scores indicate worsening disease activity.

Using change from baseline makes the endpoint a measure of how the score shifted over the follow-up interval rather than simply comparing end-of-study scores. A negative change indicates a lower score at follow-up than at baseline, while a positive change indicates a higher score. The endpoint is used to quantify disease activity across several clinical domains in a single measure. It does not show which domains account for a change, and a group mean does not describe every participant’s course.

The registry reports adjusted mean change and standard error for the primary outcome, and an ANCOVA estimate for the between-group contrast. The record does not report a threshold for a clinically meaningful ESSDAI change. Statistical evidence about a group contrast therefore should not be treated as a direct judgment about clinical importance.

7. Results Posted in the Registry

• MEDI5872 210 mg: mean -3.80 versus -2.30 on control; difference -1.50 (95% CI -3.86 to 0.86), standardized effect d = -0.47; z-test p = 0.213.

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 European League Against Rheumatism Sjogren's Syndrome Patient Reported Index (ESSPRI) Score at Day 99

• 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:
  • MEDI5872 210 mg: mean -0.60 versus -1.00 on control; difference 0.40 (95% CI -0.99 to 1.79), standardized effect d = 0.20; z-test p = 0.572.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MEDI5872 210 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering peripheral blood and minor salivary gland tissue biomarkers, focus score, patient-reported symptoms measured with ESSPRI, ESSDAI response, and adverse events. These outcomes address different aspects of disease activity, patient experience, biological measures, and safety. They do not all measure the same underlying construct, so a single common effect pattern should not be assumed.

The available numeric secondary comparison for ESSPRI does not provide clear statistical separation between the randomized groups: its interval includes zero, and the reported test result is not conventionally statistically significant. This does not establish equivalence, and ESSPRI should not be treated as interchangeable with the primary physician-assessed ESSDAI endpoint. Detailed numerical estimates for the other listed secondary measures are not reported in the registry record details available for this analysis, so a broader direction-of-effect summary across all secondary outcomes cannot be established.

Secondary endpoints can help describe whether results across different outcome types appear coherent, but they are usually less decisive when many outcomes are examined. Unless a plan addresses multiplicity, the chance of at least one apparently notable finding can increase as the number of tests grows. Multiplicity handling is not reported in the registry record. Secondary findings should therefore be read as supportive or exploratory evidence, not as independent confirmation of the primary result. The primary endpoint remains the prespecified focal outcome identified in the record, while the secondary outcomes add context without resolving the uncertainty in the primary comparison.

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

• Ratio to Baseline in Peripheral Blood Biomarkers at Day 99
• Ratio to Baseline in Minor Salivary Gland Tissue Biomarkers at Day 99
• Ratio to Baseline in Focus Score at Day 99
• Change From Baseline in European League Against Rheumatism Sjogren's Syndrome Patient Reported Index (ESSPRI) Score at Day 99
• Percentage of ESSDAI Responders at Day 99
• Number of Participants With Treatment Emergent Adverse Events (TEAEs) and Treatment Emergent Serious Adverse Events (TESAEs)
• Number of Participants With Adverse Events of Special Interest (AESIs)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s primary comparison uses analysis of covariance, or ANCOVA, and reports a net mean difference between groups. In general, ANCOVA compares outcome values across groups while accounting for one or more covariates. This can improve precision when covariates are related to the outcome. The registry identifies the method as ANCOVA, but the specific covariates, model specification, and handling of model assumptions are not reported in the registry record. It is therefore not possible to infer the complete adjustment procedure from the method label alone.

The primary outcome is continuous: it is a score, and the registry reports mean changes and standard errors. A mean describes the arithmetic average of participant-level values. A standard error describes the estimated uncertainty in a mean, rather than the spread of individual participant values. In general, a standard error becomes smaller as information increases, but its size also depends on the variability in the data. It should not be read as a range containing most participants’ outcomes.

The between-group mean difference expresses the estimated contrast on the original score scale. The sign depends on the order in which the groups are compared. For ESSDAI, lower scores indicate less disease activity, so a negative treatment-versus-placebo difference corresponds to a lower estimated change in the MEDI5872 group relative to placebo. The interpretation of an estimate must also account for whether it is adjusted or unadjusted. The sponsor’s ANCOVA estimate is adjusted according to its model; the separately calculated comparison from group summaries is a simple unadjusted re-calculation.

A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. A p-value that does not cross a conventional threshold does not prove that the groups are equivalent. It can reflect an estimate close to zero, substantial uncertainty, or both. Here, the sponsor-reported test result should be considered alongside the confidence interval and the group sizes, rather than interpreted in isolation.

A confidence interval gives a range of estimates compatible with the observed data and the method’s assumptions at its stated confidence level. In repeated use of the same method under the same assumptions, intervals constructed at a given confidence level would contain the target parameter at that rate in the long run. For an individual trial, the interval is not a probability statement that the true effect lies inside its particular endpoints. It is a practical expression of uncertainty around the estimated contrast. If an interval includes zero, the data are compatible with no group difference as well as with some differences in either direction.

The sponsor reports a 90% confidence interval for the ANCOVA result. The simple unadjusted re-calculation reports a 95% confidence interval. Confidence levels should not be conflated when comparing interval widths. The differing estimates and intervals also reflect that the sponsor’s adjusted analysis and the unadjusted re-calculation are not the same statistical calculation. The registry record does not report an explanation for choosing the sponsor analysis’s confidence level, so no reason should be inferred.

Randomization is intended in general to support fair comparison by assigning participants to groups without choosing treatment based on prognostic characteristics. Masking can reduce some forms of bias in treatment delivery, assessment, and reporting. The registry describes this study as randomized and triple-masked, but does not specify the identities of all parties covered by the masking label. The design features do not eliminate uncertainty due to small samples, missing outcome data, or limitations in the analysis record.

The registry defines the primary intent-to-treat population as all randomized and treated participants, grouped according to assigned treatment. The outcome description also says that the overall number analyzed refers to participants evaluated for that measure. These statements identify the stated population definition, but do not explain why some enrolled participants are not included in the outcome-specific analyzed counts. The detailed missing-data approach, including any imputation or sensitivity analyses, is not reported in the registry record.

The sponsor reports a superiority-type comparison. In general, a superiority test asks whether the data support a difference in a specified direction or any difference, depending on the test specification. The registry gives an ANCOVA method, a mean difference, a confidence interval, and a p-value, but does not report enough detail to reconstruct all test specifications. No equivalence or noninferiority margin is reported. Therefore, a nonsignificant superiority test cannot be reinterpreted as evidence that treatments are equivalent.

Standard errors and observed effects are also used in the separate planning illustrations. Those calculations are based on the observed effect and stated assumptions; they are not a report of the trial’s original design calculations. General sample-size planning asks how many participants would be needed to achieve a target probability of detecting an assumed effect under specified conditions. The result depends on the effect chosen, variability, allocation, significance level, and statistical model. It is not a measure of the probability that this completed trial detected an effect.

11. Confidence Intervals and Precision

The sponsor-reported 90% confidence interval for the primary ANCOVA contrast extends from -3.6 to 0.7 around a mean difference of -1.4. Because the interval includes zero, the observed data are compatible with no between-group difference as well as with a range of differences favoring either group, under the reported analysis. The point estimate alone does not convey this uncertainty.

The unadjusted re-calculation has a 95% confidence interval from -3.86 to 0.860 around a mean difference of -1.5. It is a separate calculation from the sponsor’s adjusted ANCOVA analysis, and its confidence level differs. The two intervals should not be compared as though they came from the same model and confidence level. The sponsor’s reported analysis is the primary reference for the trial’s own result.

These intervals are broad enough to leave uncertainty about the direction and size of the group difference. Their endpoints should not be interpreted as hard limits on the possible true effect. They quantify statistical uncertainty under their respective methods and assumptions; they do not account automatically for every source of uncertainty, including unreported missing-data procedures or unreported analysis choices.

The primary outcome analysis includes 16 participants in the placebo group and 13 in the MEDI5872 group. Such group sizes provide limited information for estimating a mean contrast precisely, particularly when participant outcomes vary. The registry reports standard errors for the group means but does not report the participant-level distribution. Consequently, the reported means and intervals cannot show how individual responses were distributed or whether a small number of observations had substantial influence.

The record does not report a clinically important difference threshold for ESSDAI. Precision can therefore be discussed statistically, but the interval cannot be used to decide whether all values within it would be clinically negligible or important. A useful interpretation keeps the estimated direction, interval width, sample size, and absence of a reported clinical threshold in view together.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants or total events. The record’s 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 specified as a fraction of the observed effect. These are planning illustrations computed from the observed effect, not the study’s original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the selected effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm for the same assumed effect. These are prospective planning quantities, not estimates of what the completed study achieved.

Rows that plan for a smaller fraction of the observed effect require more participants because smaller differences are harder to distinguish from random variation. The illustration therefore makes the assumed effect size visible as a key driver of sample-size requirements. Since the observed effect itself is uncertain, planning around it does not establish that the same effect would occur in another study.

This is not observed power. It should not be used to assess the probability that the trial’s actual result is correct or to replace interpretation of its estimate and confidence interval. The registry record does not report the original sample-size justification, so the planning display cannot be treated as evidence of the rationale used when the trial was designed.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.500; pooled standard deviation σ = 3.220.
2. n = 2 × (1.96 + 0.842)² × 3.220² / -1.500² = 72.3, rounded up to 73 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
delta <- -1.5                      # observed difference in means
sigma <- 3.22007591352889                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2334306)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 73 (80% power), 97 (90% power)
 75% of observed effect: n per arm = 129 (80% power), 173 (90% power)
 50% of observed effect: n per arm = 290 (80% power), 388 (90% power)
power.t.test: 73.3 
Simulated power at n = 73 per arm: 0.805 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 comparison using ANCOVA: a net mean difference of -1.4, a 90% confidence interval from -3.6 to 0.7, and p = 0.262. This is the trial’s reported primary analysis and should be distinguished from a simple re-calculation based on the posted group summaries.

The re-calculation gives an unadjusted mean difference of -1.5, a 95% confidence interval from -3.86 to 0.860, and an unadjusted p-value of 0.213. It does not reproduce the sponsor’s ANCOVA model, and its confidence interval uses a different confidence level. Small discrepancies between these summaries are not a reason to replace the sponsor’s analysis with the unadjusted calculation. The sponsor’s own analysis takes precedence.

Both analyses describe an uncertain group contrast, and both confidence intervals include zero. The re-calculation is useful as a transparent check based on the posted summary statistics, but it cannot recover unreported model details or participant-level information. The registry record does not provide enough detail to independently reproduce the ANCOVA estimate in full.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple secondary outcomes and reports multiple analyses. It does not report whether the statistical plan used a multiplicity adjustment, a hierarchical testing procedure, or another approach to control the chance of false-positive findings across outcomes. Without that information, individual secondary p-values should be interpreted cautiously. When many hypotheses are tested, some results may appear unusual by chance even if there are no true effects; adjustment procedures are one general way to address that issue.

The record defines the primary intent-to-treat population as randomized and treated participants analyzed by assigned treatment. It reports outcome-specific analyzed counts for the primary endpoint, but does not explain the difference between total enrollment and the numbers evaluated for that measure. The reasons for missing outcome measurements, withdrawals, or exclusions from a particular analysis are not reported in the registry record.

The method used to handle missing data is also not reported. In general, a complete-case analysis, imputation, or a model-based approach can rely on different assumptions about why observations are missing and what those unobserved values might have been. Without the analysis details, it is not possible to assess how missing outcomes were handled or whether sensitivity analyses examined alternative assumptions.

The registry names ANCOVA for the primary comparison but does not report the specific covariates, model diagnostics, or all analysis specifications. It also does not report whether subgroup analyses or interim analyses were planned or conducted. These details should not be inferred from a method label or from the completed status of the study. The available result is interpretable as a reported ANCOVA comparison, but the record does not support a full audit of the statistical plan or its implementation.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: small intestine polyp (3.2%).

The registry reports serious adverse events among participants at risk: zero in the placebo group, whose serious-event risk group included 16 participants, and one among the 31 participants categorized as having any MEDI5872 210 mg exposure. The record lists small intestine polyp as the top serious-event term, with 3.2%. It reports zero deaths in both categories.

These safety categories should be read in light of the study’s crossover to open-label MEDI5872. The “any MEDI5872” group reflects exposure rather than a simple comparison by original randomized assignment, and includes more participants than the randomized MEDI5872 group analyzed for the primary endpoint. The figures therefore do not form a direct randomized safety contrast across the full trial period.

The registry also reports other adverse events in 14 of 16 participants in the placebo category and 29 of 31 participants in the any-MEDI5872 category. Counts alone do not establish whether an event was caused by treatment, and the small numbers do not support strong comparative conclusions. The registry record does not provide the event-level context needed to assess timing, severity beyond the reported categories, or causality. These are descriptive safety summaries, not evidence of a treatment effect.

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

The posted primary result estimates a group difference in change in ESSDAI by Day 99, with a point estimate in the direction of a larger score reduction for MEDI5872 than for placebo. The sponsor-reported confidence interval includes zero and spans values on both sides of it. The result therefore does not clearly distinguish a between-group difference from no difference in this analysis.

This does not show that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the plausible difference is contained within that margin; neither is reported in the registry record. Nor does a nonsignificant result prove that an effect is absent. The interval allows for uncertainty about both the size and direction of the contrast.

The score measures physician-assessed disease activity across several domains, but a group mean does not reveal how individual participants changed or which domains contributed to the mean. The registry record does not report a clinically important change threshold, so the statistical estimate cannot be directly classified as clinically meaningful or unimportant from the available information.

The finding applies to the analyzed participants, outcome, treatment regimen, and Day 99 comparison described in the record. It does not establish effects at other time points or for other patient groups. The record also does not provide complete details about missing-data handling, the full ANCOVA specification, or multiplicity procedures. Those gaps limit how far the posted comparison can be generalized beyond its stated analysis.

In short, the result is an imprecise estimate from a small Phase 2a study, with no clear statistical separation in the sponsor-reported primary comparison. It is neither proof of benefit nor proof of no effect. Its appropriate role is to describe the evidence and uncertainty available from this trial, without replacing a broader assessment of evidence or a clinical judgment.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a significance test are not enough to interpret a clinical comparison. The estimated direction favors a larger reduction in ESSDAI for MEDI5872, but the interval also includes zero and the reported test does not provide clear evidence of a difference. Considering both the estimate and its precision avoids turning a single test result into a binary conclusion.

It also illustrates the importance of distinguishing adjusted sponsor analyses from simple calculations using summary statistics. The ANCOVA result is the trial’s reported primary analysis, while a summary-statistic re-calculation provides a separate, unadjusted view. Their similar broad uncertainty does not make them the same model, and the sponsor’s reported analysis remains the main reference for the trial result.

The study’s outcome-specific sample sizes are modest relative to the total enrollment, and the record does not explain why fewer participants were evaluated for the primary endpoint than were enrolled. This makes analysis-population definitions and missing-data reporting important parts of interpretation. The record provides a population definition, but not the detailed participant flow or missing-data procedures needed to assess those issues fully.

Finally, the study has several distinct secondary outcome domains and a safety summary that includes open-label exposure. This demonstrates why multiplicity and exposure definitions matter: secondary endpoints should not be treated as repeated confirmations, and exposure-based safety categories should not be mistaken for randomized comparisons. These statistical distinctions help readers describe the evidence accurately while keeping uncertainty visible.

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 outcome analysis includes 16 participants in the placebo group and 13 in the MEDI5872 group. These analyzed group sizes limit precision, as reflected in the confidence interval that includes zero. The reason that the endpoint-specific counts differ from total enrollment is not reported in the registry record, leaving uncertainty about participant flow and outcome availability.

The registry reports ANCOVA but does not specify the model covariates, full analysis specification, or diagnostic checks. The sponsor’s result therefore cannot be fully reconstructed from the registry summary. The simple unadjusted re-calculation is not a substitute for that missing detail and should not be treated as the primary result.

The original sample-size calculation and its assumptions are not reported. Planning illustrations based on the observed effect cannot establish the original rationale or show what target difference the trial was designed to detect. The record also does not report a clinically important difference threshold for ESSDAI.

Multiplicity handling across the primary and secondary outcomes is not reported. The missing-data approach and sensitivity analyses are not reported either. These omissions make it difficult to assess the robustness of results to multiple testing or to assumptions about participants without outcome measurements.

The study includes an open-label period in which the placebo-assigned group began receiving MEDI5872. Safety summaries organized by any exposure to MEDI5872 therefore do not represent a simple comparison by original assignment over the whole study. Finally, detailed numeric results for several listed secondary endpoints are not reported in the record information, limiting assessment of consistency across outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 2a, Randomized, Placebo Controlled, Study to Evaluate the Safety and Efficacy of AMG 557/MEDI5872 in Primary Sjögren's Syndrome — NCT02334306.
• Registry record last updated 2019-03-19; status last verified 2019-02.
• Results first posted 2019-03-19.
• 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

NCT02334306 is a completed, randomized, triple-masked, parallel-group Phase 2a placebo-controlled study of MEDI5872 in primary Sjögren's syndrome, sponsored by MedImmune LLC. The registry reports enrollment of 32 participants and a primary outcome of change from baseline to Day 99 in ESSDAI score.

The sponsor’s ANCOVA comparison reports a mean difference of -1.4, with a 90% confidence interval from -3.6 to 0.7 and p = 0.262. The interval includes zero, so the primary result does not clearly distinguish a group difference from no difference. The registry also describes an open-label period and lists multiple secondary outcomes.

Interpretation is limited by small outcome-specific groups and by registry entries that are not reported, including the original sample-size rationale, missing-data procedures, multiplicity handling, and complete ANCOVA specification. The result is an uncertain estimate, not proof of benefit, absence of effect, or equivalence.