A Study Evaluating the Effectiveness of AMG 334 Injection in Preventing Migraines in Adults Having Failed Other Therapies: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Evaluating the Effectiveness of AMG 334 Injection in Preventing Migraines in Adults Having Failed Other Therapies (NCT03096834), a randomized phase 3 study. The primary outcome is Percentage of Participants With at Least 50% Reduction From Baseline of Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment).

2. Clinical Question

The clinical question is about a defined response threshold over the final 4 weeks of the 12-week double-blind treatment period, not simply whether the average number of migraine days changed. That threshold makes the outcome a binary response: each participant either met the reduction criterion or did not. The registry also lists secondary questions about changes in monthly migraine days, migraine-related physical function, acute migraine-specific medication treatment days, larger reductions in migraine days, and anti-AMG334 antibodies.

The comparison is randomized and double-blind, so treatment assignment was intended to be allocated by chance and masked during the blinded period. The registry record describes a placebo-controlled parallel-group study. The recorded primary result is a comparison between the AMG334 140 mg and placebo groups; it does not establish how the treatment would compare with other preventive therapies or in people outside the stated study population.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group, multicenter study of AMG334 versus placebo. It enrolled 246 participants and is recorded as completed. Its official title describes a 12-week comparison of once-monthly subcutaneous AMG334 140 mg against placebo in adults with episodic migraine who had failed 2-4 prophylactic treatments. The record lists Novartis Pharmaceuticals as sponsor.

During the double-blind period, the active regimen was two subcutaneous injections of AMG334 70 mg, administered every 4 weeks. The placebo group received matching subcutaneous injections on the same schedule. The primary outcome was assessed at Month 3, using the last 4 weeks of treatment. The primary analysis population is identified as the full analysis set, but the registry record does not report a further definition of that population in the results information.

The record also describes open-label extensions in which participants originally assigned to AMG334 continued AMG334 and participants originally assigned to placebo switched to AMG334. Those later treatment groups appear in the safety information, but the primary efficacy comparison described in the result is the double-blind comparison. The registry record does not report enough detail to characterize the open-label period’s duration or to treat it as part of the randomized primary efficacy comparison.

The record lists a study start date of 2017-03-20 and a primary completion date of 2018-01-18. Those dates identify the registry milestones; they do not by themselves describe how long each participant was followed. The trial’s original sample-size justification, original statistical analysis plan, and any interim analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 333 participants were screened for the trial

Double-Blind Treatment Epoch

Reasons for not completing this period:

Open-Label Treatment Epoch

Reasons for not completing this period:

Safety Follow-Up Epoch

Reasons for not completing this period:

Post-Trial Access Epoch

Analysis population for the primary outcome, as defined in the registry: Full analysis set

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 Percentage of Participants With at Least 50% Reduction From Baseline of Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment), measured over Baseline, Month 3 (last 4 weeks of treatment).

The primary endpoint is the percentage of participants with at least a 50% reduction from baseline in monthly migraine days during the last 4 weeks of treatment, assessed at Month 3. It converts each participant’s change into a response classification and then compares the proportion meeting the threshold between treatment groups. This differs from comparing mean changes: it focuses on the share reaching a prespecified level of improvement rather than the average change across the group.

The registry defines a migraine day using headache features and associated symptoms. A qualifying headache could be with or without aura, last at least 30 minutes, and meet at least one listed symptom or pain-feature criterion. A day was also counted when a migraine-specific medication such as a triptan or ergotamine was taken during aura or headache, regardless of duration and the specified pain features or associated symptoms.

As a general statistical point, a response threshold can be easier to interpret as a proportion of participants crossing a stated boundary, but it discards information about how far each person’s change lies above or below that boundary. Participants just short of the threshold and participants with no reduction are both counted as nonresponders. The continuous secondary outcome for change in monthly migraine days provides a different view of the outcome distribution, but it does not replace the primary responder question.

The endpoint gives a short-term comparison at the end of the blinded treatment period. It does not, by itself, describe persistence of response after that period, long-term outcomes, or the distribution of individual responses within each group.

7. Results Posted in the Registry

• AMG334 140 mg DB: 30.3% (36/119) versus 13.7% (17/124) on control; risk difference 16.5 percentage points (95% CI 6.3 to 26.8), risk ratio 2.21 (1.31–3.71); unadjusted two-proportion z-test p = 0.002.

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 Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment)

• 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:
  • AMG334 140 mg DB: mean -1.75 versus -0.16 on control; difference -1.59 (95% CI -2.75 to -0.43), standardized effect d = -0.35; z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AMG334 140 mg DB than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in the Number of Monthly Acute Migraine-specific Medication Treatment Days at Month 3

• 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:
  • AMG334 140 mg DB: mean -1.25 versus 0.46 on control; difference -1.71 (95% CI -2.43 to -0.99), standardized effect d = -0.60; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AMG334 140 mg DB than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With a 75% Reduction From Baseline of Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • AMG334 140 mg DB: 11.8% (14/119) versus 4.0% (5/124) on control; risk difference 7.7 percentage points (95% CI 1.0 to 14.5), risk ratio 2.92 (1.08–7.85); unadjusted two-proportion z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for AMG334 140 mg DB than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the picture beyond the primary responder threshold. They cover change in monthly migraine days, physical impairment and everyday activities, acute migraine-specific medication treatment days, more demanding migraine-day reduction thresholds, and anti-AMG334 antibodies. Together, the posted efficacy summaries generally point in a direction consistent with the primary result during the double-blind period: the active-treatment group’s summaries are more favorable on the migraine-day and medication-use measures, and the higher-response thresholds also show a similar broad pattern. The functional outcome and antibody outcome address different questions and should not be collapsed into the primary efficacy conclusion.

Secondary endpoints can help show whether an observed primary result is accompanied by changes in related outcomes, but they are not automatically independent confirmations. Several outcomes can be examined in one study, and the chance of at least one apparently notable result can increase when many hypotheses are tested. The registry record does not report whether multiplicity adjustment was used for the secondary results, so nominal p-values should be read cautiously and in the context of the full set of analyses.

The outcomes also differ in scale and meaning. A continuous change in monthly days describes an average change, while a responder percentage counts participants crossing a threshold. Medication-treatment days and function scores concern related but distinct aspects of the experience. Agreement across these measures can add context, but differences among them are not necessarily contradictory. Each analysis may use a different statistical method and analysis population, and the registry summaries do not provide enough detail to assess every modeling choice or missing-data assumption.

The secondary results are best regarded as supportive and exploratory unless the full analysis plan establishes their role and multiplicity handling. They add context to the primary finding but do not expand the primary endpoint’s time frame or establish long-term effects.

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

• Change From Baseline in Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment)
• Change From Baseline in Physical Impairment and Everyday Activities as Measured by the Migraine Physical Function Impact Diary (MPFID) at Month 3
• Change in the Number of Monthly Acute Migraine-specific Medication Treatment Days at Month 3
• Percentage of Participants With a 75% Reduction From Baseline of Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment)
• Percentage of Participants With a 100% Reduction From Baseline of Monthly Migraine Days (MMD) in the Last Month (Last 4 Weeks of Treatment)
• Number of Participants Who Developed Anti-AMG334 Antibodies

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary odds ratio describe?

The primary outcome is binary because each participant is classified according to whether the 50% reduction threshold was reached. The sponsor reported an odds ratio comparing the odds of meeting that threshold in the AMG334 group with the odds in the placebo group. An odds ratio above 1 indicates higher observed response odds in the first group under that comparison. It is not the same quantity as a risk ratio or a difference between response percentages, and it should not be read as a direct multiplier of the percentages themselves.

The sponsor used a Cochran-Mantel-Haenszel analysis. In general, this method estimates an association across strata and can account for stratification factors when those factors are part of the analysis. The registry result does not identify the strata or provide enough detail to reconstruct the exact analysis. The reported odds ratio and confidence interval should therefore be read as the sponsor’s stated analysis, not as a fully reproducible description of every model choice.

What does the unadjusted recalculation add?

The recalculation is a simple, unadjusted comparison based on the posted response counts and group sizes. For a binary endpoint, one useful summary is the risk difference, which expresses the difference between the two response proportions on the probability scale. Another is the risk ratio, which compares the proportions as a ratio. These summaries answer related but not identical questions to the odds ratio. The recalculation is descriptive and does not reproduce any stratification or adjustment used by the sponsor. Because the registry record does not mark a discrepancy, it is reasonable to describe the recalculation as broadly consistent with the reported result, while keeping the sponsor’s own analysis as the formal trial analysis.

In general, an unadjusted recalculation may be useful for checking the direction and scale of a posted result, but it cannot recover participant-level details or adjust for factors not represented in the summary data. It should not be mistaken for a new clinical trial analysis. No new estimate should be inferred by combining or transforming the different reported effect measures.

How should the p-value be read?

The reported p-value of 0.002 is associated with the sponsor’s primary comparison. In general, a p-value is calculated under a statistical model that assumes a specified null hypothesis, often no group difference. It describes how unusual data at least as incompatible with that null model would be if the model and its assumptions held. It does not give the probability that the treatment has no effect, and it does not quantify the chance that the result will replicate.

A p-value also does not measure how important a result is. The responder percentages and odds ratio describe the observed contrast, while the confidence interval conveys uncertainty about the estimated effect. Statistical evidence, effect size, precision, clinical context, and limitations all need to be considered together. A nominal p-value for a secondary outcome is especially difficult to interpret when the number of outcomes tested and any multiplicity procedure are not known.

Why can the analysis method matter?

Analysis methods can differ because they use different scales, handle stratification differently, or make different assumptions about the outcome and missing observations. For binary outcomes, odds, risks, and risk differences are distinct measures. For continuous outcomes, a mean difference describes a difference in group averages. In general, an adjusted model may not produce the same estimate as a simple comparison of summary values, even when both use the same treatment groups.

The continuous secondary outcomes were reported using mixed models analysis. In general, mixed models can use repeated measurements and account for correlation among observations from the same participant, depending on model specification. The registry record does not report the full model specification, covariance structure, covariates, or missing-data assumptions, so those details cannot be assessed from the listed result alone. Standard errors reported for group means describe uncertainty around those means under the relevant analysis, but they are not the same as standard deviations describing person-to-person spread.

Why does over-dispersion matter in count outcomes?

As a general statistical concept, over-dispersion occurs when count data vary more than a model’s assumed distribution allows. If ignored, standard errors can be too small and confidence intervals too narrow, potentially making evidence appear more precise than it is. Count outcomes such as monthly migraine days may have skewness, excess zeros, or variability not captured by a simple model. A suitable analysis depends on the data structure and prespecified approach. The registry record’s result summaries do not provide enough information to determine whether over-dispersion was assessed or how it was handled.

The primary responder endpoint is binary rather than a count model, so this concept does not directly define the primary odds-ratio analysis. It is relevant as a general consideration when interpreting count-based outcomes and selecting analyses for monthly days or medication-treatment days. The registry record does not report a specific over-dispersion assessment for those outcomes.

What information is needed to reproduce the analyses?

Reproduction would require more than the brief outcome summaries: details such as the analysis population definition, handling of missing outcome data, model covariates, stratification factors, and any sensitivity analyses would be needed. These are not reported in the registry record information. The posted participant counts and aggregate outcome values allow simple recalculations, but not a reconstruction of participant-level modeling or all sponsor analyses.

11. Confidence Intervals and Precision

The sponsor-reported primary odds ratio is 2.73, with a 95% confidence interval from 1.43 to 5.19. The interval excludes 1, the value that corresponds to equal odds under this measure, and the reported p-value is 0.002. This combination is consistent with evidence of a difference under the sponsor’s stated analysis. It does not mean that the true odds ratio has a 95% probability of lying inside this particular interval; in general, a 95% confidence procedure is expected to cover the fixed underlying parameter in 95% of repeated samples when its assumptions hold.

The interval spans a range of effect magnitudes, so the point estimate should not be treated as known exactly. The lower and upper limits reflect sampling uncertainty under the analysis. Confidence intervals do not capture every uncertainty, such as unreported modeling decisions, measurement limitations, or limitations in how well the trial population represents other settings.

The posted response percentages are 30.3% for AMG334 and 13.7% for placebo. Those are observed group summaries, not precise predictions for a future population. The recalculated unadjusted comparison also includes an interval for the risk-difference scale, but it is distinct from the sponsor’s odds-ratio interval. Confidence intervals on different scales answer different questions and should not be directly substituted for one another.

In general, precision depends on the amount of information in the data, the outcome’s variability, and the analysis method. A confidence interval that is narrower conveys greater statistical precision for that estimand, but precision does not ensure absence of bias or guarantee that an effect is clinically meaningful. The registry record does not report a prespecified threshold for clinical importance.

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 illustrations are expressed as participants per arm for the binary primary outcome and other non-time-to-event outcomes. Time-to-event planning results, when present, would be expressed as total events, but the listed outcomes in this study are not time-to-event outcomes. For the primary comparison, the illustration based on 100% of the observed effect gives 98 participants per arm for 80% power and 130 participants per arm for 90% power. Planning for 75% of the observed effect gives 162 participants per arm for 80% power and 216 participants per arm for 90% power. Planning for 50% of the observed effect gives 336 participants per arm for 80% power and 449 participants per arm for 90% power.

In plain terms, the 80% power column describes the estimated number of participants per arm under the stated planning assumptions to have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. These are conditional planning calculations, not guarantees about the outcome of a future study. This is not observed power.

The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each effect scenario is a stated fraction of the observed effect. Smaller effects require more participants to be detected with the same target power under these assumptions. These illustrations were computed from the observed effect and are not the trial’s own original design calculation. The trial’s original sample-size assumptions and justification are not reported in the registry record. The illustrations should therefore not be read as evidence about the sponsor’s original planning process or as a reconstruction of it.

A planning curve based on the same assumptions represents how the estimated participant requirement changes as the effect to detect changes. It is conditional on the observed effect used as its starting point and on the same statistical assumptions; it does not show the trial’s observed probability of success. Planning results can be sensitive to the assumed effect, and an effect estimated in one study may not be the effect a future study should expect.

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 = 0.137; treatment proportion p₁ = 0.303; average p̄ = 0.220.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5856 = 1.1479.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5738 = 0.4830.
4. n = (1.1479 + 0.4830)² / (0.1654)² = 97.2, rounded up to 98 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 <- 0.137096774193548                          # control proportion
p1 <- 0.302521008403361                          # 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(3096834)
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 = 98 (80% power), 130 (90% power)
 75% of observed effect: n per arm = 162 (80% power), 216 (90% power)
 50% of observed effect: n per arm = 336 (80% power), 449 (90% power)
power.prop.test: 97.2 
Simulated power at n = 98 per arm: 0.818 (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 sponsor’s primary analysis is reported as a Cochran-Mantel-Haenszel odds ratio of 2.73, with a 95% confidence interval from 1.43 to 5.19 and p = 0.002. The posted response percentages were 30.3% with AMG334 and 13.7% with placebo. The unadjusted recalculation uses the posted group counts and produces an effect summary on a different scale, including a risk difference rather than the sponsor’s odds ratio. These measures should not be expected to have identical numerical values because they describe the comparison differently.

The registry record does not flag a discrepancy between the sponsor result and the recalculated result. Their direction and statistical interpretation are consistent in the posted summaries. The recalculation is a simple check from aggregate data; it does not reproduce the sponsor’s analysis method or any analysis adjustments. For interpretation of the trial’s primary result, the sponsor’s reported analysis takes precedence as the trial’s own analysis. The difference in scales is a reason to keep the measures clearly labeled, not evidence of a contradiction.

The same distinction applies to secondary continuous outcomes: simple recalculations from posted means are not equivalent to the sponsor’s mixed models analysis. The registry reports both types of summaries, and they should be described as separate analyses rather than treated as interchangeable estimates.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and several secondary outcomes, with multiple analyses reported. Testing multiple outcomes creates a multiplicity issue: as a general statistical matter, the chance of obtaining at least one nominally small p-value can rise when many hypotheses are tested. A prespecified hierarchy, family-wise error procedure, or other multiplicity strategy can address this issue, but the registry record does not report whether such a strategy was used for the secondary outcomes. The primary analysis should be distinguished from secondary results whose multiplicity status is unclear.

The record identifies the primary analysis population as the full analysis set, but it does not report a detailed definition of that set in the results information. It also does not report how missing primary or secondary outcome measurements were handled, whether participants with missing outcomes were excluded or imputed, or what sensitivity analyses were performed. These choices matter because conclusions can depend on which randomized participants contribute to an analysis and on assumptions about unobserved outcomes.

The registry record does not report the full statistical analysis plan, the original sample-size justification, interim analyses, or the specific covariates and stratification factors used in each model. It does not provide sufficient detail to determine whether the outcomes or analysis choices were changed during the study. Those items should be treated as not reported in the registry record, rather than inferred from the result summaries.

In general, a complete assessment of multiplicity and missing data requires the prespecified analysis plan and its implementation, not only the reported endpoint estimates. The absence of those details in the registry record limits independent evaluation of how robust the results are to alternative analysis decisions. It does not invalidate the reported result, but it narrows what can be concluded from the registry summaries alone.

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: migraine (1.7%), depression (1.6%), dacryostenosis acquired (0.8%), inflammation of lacrimal passage (0.8%), retinal vein thrombosis (0.8%).

During the double-blind comparison, serious adverse events were reported for 2 of 119 participants in the AMG334 group and 1 of 124 participants in the placebo group. Other adverse events were reported for 44 of 119 and 43 of 124 participants, respectively. No deaths were reported in either double-blind group. These are counts from the registry safety summary; they do not by themselves establish whether an event was caused by treatment.

The record also lists serious adverse event information for the open-label groups: 16 of 118 in the group continuing AMG334 and 18 of 122 in the group switching from placebo to AMG334. Other adverse events were reported for 94 of 118 and 101 of 122, respectively, and no deaths were reported in either group. These open-label figures should be kept separate from the randomized double-blind comparison because participants’ treatment histories and the study period differ.

The listed serious-event terms include migraine and several other conditions. Such term listings describe events recorded in the registry and should not be interpreted as proof of treatment causation or as a complete assessment of comparative safety. The registry summary does not provide enough information to evaluate event timing, severity beyond the serious classification, exposure-adjusted rates, or the investigators’ causal assessments.

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

The primary result shows that, in this randomized double-blind study, a larger percentage of participants assigned to AMG334 met the registry-defined 50% reduction threshold for monthly migraine days than participants assigned to placebo. The sponsor-reported odds ratio and its confidence interval indicate a difference in the observed response odds under the stated analysis. The result is specific to the studied adults with episodic migraine who had failed 2-4 prophylactic treatments and to the Month 3 assessment period.

It does not establish how long any response lasts beyond the last 4 weeks of the 12-week treatment period. It does not compare AMG334 with another active preventive treatment, establish the best treatment for an individual, or show that every participant benefits. A group percentage does not reveal the full distribution of individual changes. The trial result also does not establish effects in populations not represented by the stated eligibility description.

The reported p-value is not the probability that the finding is due to chance, and the confidence interval does not account for every possible source of uncertainty. The registry record does not report the full details needed to assess missing-data handling, multiplicity adjustment, model specifications, or the original sample-size rationale. Those gaps limit independent assessment of robustness, especially for secondary outcomes.

Safety counts are descriptive and do not establish causation. The open-label safety groups should not be combined with the blinded comparison to infer a randomized safety contrast. The result should therefore be read as evidence about a defined short-term, placebo-controlled comparison—not as a complete account of longer-term benefit, comparative effectiveness, or safety in all clinical settings.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a randomized, double-blind, placebo-controlled design with a clearly defined responder endpoint. The primary outcome asks how often participants crossed a meaningful percentage-reduction threshold, while the secondary outcomes examine average changes and related measures. That mix illustrates why endpoint choice matters: a responder analysis and a mean-change analysis summarize different features of the same general clinical domain.

The result also illustrates the distinction between an effect estimate and its precision. The odds ratio summarizes the relative odds under the sponsor’s method, while the confidence interval shows that the estimate remains uncertain. A p-value adds information about compatibility with a null model but does not measure importance or guarantee replication. Reading these quantities together is more informative than treating any one as a complete conclusion.

Another statistical lesson is that aggregate-data recalculations can check the broad direction of a reported result without reproducing the original model. The registry’s sponsor analysis and simple unadjusted calculations are different summaries; clear labeling prevents confusion between them. Similarly, planning illustrations based on an observed effect are not the same as the assumptions that originally determined a trial’s enrollment target.

Finally, multiple secondary outcomes, missing-data decisions, and analysis-population definitions affect how confidently a result can be interpreted. The registry summaries provide useful estimates but do not report every detail needed for full independent reconstruction. Statistical interpretation therefore includes both what the trial estimates and what its record leaves uncertain.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary result concerns a short assessment window: the last 4 weeks of a 12-week double-blind treatment period. The registry record does not establish durability beyond that window. The population is adults with episodic migraine who had failed 2-4 prophylactic treatments, so the result should not automatically be generalized to people with different migraine patterns, treatment histories, or eligibility characteristics.

The primary endpoint is a threshold-based responder measure. It communicates the proportion reaching the 50% reduction criterion but does not show how far each participant’s migraine days changed or how outcomes varied within the responder and nonresponder groups. The continuous secondary outcome provides a complementary summary, but it too is an aggregate measure.

The registry record does not report the detailed definition of the full analysis set, the handling of missing endpoint data, the full model specifications, or the multiplicity strategy for secondary outcomes. These omissions limit assessment of whether alternative analytic decisions would change the estimates or their uncertainty. The original sample-size assumptions and any interim analyses are also not reported in the registry record.

The safety summaries are counts rather than a complete causal assessment. The open-label safety groups have different treatment histories from the double-blind groups and should not be interpreted as a continuation of the randomized comparison. The record does not provide enough detail to assess event timing, exposure-adjusted rates, or longer-term safety. These limitations do not negate the posted findings, but they define the boundaries of what the registry results establish.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Evaluating the Effectiveness of AMG 334 Injection in Preventing Migraines in Adults Having Failed Other Therapies — NCT03096834.
• Registry record last updated 2022-03-23; status last verified 2022-02.
• Results first posted 2022-02-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes NCT03096834, a completed Phase 3 randomized, double-blind, multicenter, parallel-group study sponsored by Novartis Pharmaceuticals. It compared monthly subcutaneous AMG334 140 mg, given as two 70 mg injections every 4 weeks, with matching placebo in adults with episodic migraine who had failed 2-4 prophylactic treatments.

The primary outcome was the percentage of participants with at least a 50% reduction from baseline in monthly migraine days during the last 4 weeks of treatment at Month 3. The sponsor reported a Cochran-Mantel-Haenszel odds ratio of 2.73, with a 95% confidence interval from 1.43 to 5.19 and p = 0.002. The registry also lists secondary efficacy and safety outcomes. Important details—including missing-data handling, multiplicity procedures, and the original sample-size justification—are not reported in the registry record.