Study to Assess in Home Use of Evolocumab (AMG 145) Administration Using Either an Automated Mini-doser or a Prefilled Autoinjector/Pen: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess in Home Use of Evolocumab (AMG 145) Administration Using Either an Automated Mini-doser or a Prefilled Autoinjector/Pen (NCT01879319), a randomized phase 3 study. The primary outcome is Percentage of Participants With Full Administration of Evolocumab at Both Weeks 4 and 8.

2. Clinical Question

3. Trial Design

The registry identifies this as a completed, randomized Phase 3 study with a parallel-group model and no masking. The study was multicenter and enrolled participants with primary hypercholesterolemia or mixed dyslipidemia. Its stated objective was to assess users’ ability to administer a full dose of evolocumab in a home-use setting using an automated mini-doser or an autoinjector/pen. The registry lists enrollment of 164 and reports 82 participants in each arm for the primary outcome.

Both groups received evolocumab 420 mg once a month for 8 weeks, with administrations scheduled on Day 1, Week 4, and Week 8. The AMD arm used one 3.5 mL injection; the AI/pen arm used three 1.0 mL injections. Participants self-administered in the clinic on Day 1 under supervision and then at home. The available arm descriptions are truncated after the home-use wording, so further details of the home-use procedure are not reported in the registry record.

The primary outcome was full administration at both Weeks 4 and 8. Participants were asked in telephone interviews about attempted injections and whether each was administered in part, in full, or not at all. The registry notes that only full administrations occurring inside the prespecified visit window counted. A secondary outcome assessed percent change from baseline in LDL-C at the mean of Weeks 10 and 12.

The study began on 2013-07-11, had primary completion on 2013-11-15, and is marked completed. The registry record does not report masking because the study was unmasked, nor does it give further detail on randomization procedures, allocation concealment, or the original sample-size justification.

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: Randomization was stratified on the basis of screening LDL-C concentration (\< 130 mg/dL \[3.4 mmol/L\] or ≥ 130 mg/dL). Participants were trained by study site staff to prepare and self-administer the study drug.

Overall Study

Reasons for not completing this period:

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.

Population: Full analysis set (all randomized participants who received at least 1 dose of study drug).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Full Administration of Evolocumab at Both Weeks 4 and 8, measured over Weeks 4 and 8.

The primary endpoint is the percentage of participants with full administration of evolocumab at both Weeks 4 and 8. For each visit, a telephone interview assessed attempted injections and whether administration was full, partial, or absent. Only full administrations within the prespecified visit window counted toward the endpoint. The analysis population is identified as the full analysis set.

This endpoint is relevant to the stated objective because the study compared home-use administration devices. It captures completion at both specified visits, rather than success at either visit alone or a broader measure of treatment adherence. A participant needed full administration at both time points to meet the endpoint definition. The registry does not report how interview responses were verified or how incomplete, missed, or out-of-window reports were handled beyond the rule that only full administrations inside the visit window were included.

The primary outcome is binary at the participant level: a participant either met the full-administration definition at both visits or did not. Reporting the percentage in each arm allows a direct description of the frequency of that outcome, while a treatment difference and its confidence interval describe the estimated contrast and its uncertainty. This measure does not quantify the amount of medication delivered when an injection was partial, nor does it describe the reason for an incomplete administration. It also does not directly measure LDL-C response, which is assessed separately as a secondary outcome.

7. Results Posted in the Registry

• Evolocumab AI/Pen: 91.5% (75/82) versus 93.9% (77/82) on control; risk difference -2.4 percentage points (95% CI -10.4 to 5.5), risk ratio 0.97 (0.89–1.06); unadjusted two-proportion z-test p = 0.549.

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.

Percent Change From Baseline in LDL-C at the Mean of Weeks 10 and 12

• 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:
  • Evolocumab AI/Pen: mean -64.50 versus -67.90 on control; difference 3.40 (95% CI -3.25 to 10.05), standardized effect d = 0.16; z-test p = 0.316.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Evolocumab AI/Pen and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: percent change from baseline in LDL-C at the mean of Weeks 10 and 12. The overall pattern is a reduction from baseline in both arms. The estimated treatment difference has a confidence interval that includes zero, so this result does not show a statistically clear separation between the delivery-device groups for this secondary measure.

The secondary outcome addresses a different question from the primary endpoint. The primary result concerns whether participants reported full administration at both home-use visits; the secondary result concerns LDL-C change. The LDL-C findings therefore add a measure of biological response but do not directly confirm or overturn the primary finding about administration completion. They also do not establish that the devices produce identical responses.

Unadjusted secondary results carry less inferential weight when several outcomes or comparisons are considered, because the chance of at least one apparently notable result can increase across multiple tests. General: multiplicity procedures can control that risk, but they need to be specified and reported to interpret adjusted claims. The registry record does not report a multiplicity plan, adjustment, or confirmatory hierarchy for the secondary outcome. The posted secondary analysis should therefore be treated as supportive descriptive evidence rather than as a stand-alone definitive finding.

The registry reports least-squares means and standard errors, but does not identify the model terms or adjustments behind those estimates. That limits independent assessment of the analysis. No additional secondary endpoint results are posted in the registry record, so conclusions about other outcomes are not available.

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

• Percent Change From Baseline in LDL-C at the Mean of Weeks 10 and 12

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results include arm-level percentages, confidence intervals, and a recalculated unadjusted comparison. The sponsor also reported its own treatment difference. These quantities answer related but not identical questions: arm percentages describe each group, while a treatment difference estimates the contrast between groups. The registry does not name the method used for the sponsor’s analysis.

What does a confidence interval communicate?

General: a confidence interval expresses uncertainty around an estimate under the assumptions of the analysis. A narrower interval represents greater precision, while a wider interval leaves a broader range of values compatible with the data and method. It is not a range containing a fixed proportion of individual participant outcomes, and it does not give the probability that the true effect lies within its particular limits.

For a difference, the value representing no difference is zero. When an interval includes zero, the data do not rule out no difference at the confidence level used. That does not prove the groups are identical. It also does not mean every value inside the interval is equally plausible. Interpretation should consider the estimate, the limits, the outcome’s meaning, and the study’s design together.

How should the primary contrast be read?

The recalculated risk difference compares the proportion meeting the endpoint in AI/pen with the proportion in AMD. A negative estimate means the observed proportion was lower in AI/pen under this subtraction order; a positive estimate would mean it was higher. The estimate is unadjusted, meaning it is calculated from the posted arm-level summaries without covariate adjustment. The registry’s reported analysis expresses its result as a treatment difference in percentage points, and its confidence interval also crosses zero.

The recalculated unadjusted p-value tests a null hypothesis of no difference under the calculation’s assumptions. A p-value is not the probability that the null hypothesis is true, nor a measure of clinical importance. The registry does not give a p-value for the sponsor’s analysis, so the two analyses should not be presented as if they share identical inferential output.

Why can estimates differ in presentation?

Arm-level displayed percentages may be rounded, while a treatment contrast can be formed from underlying counts or from a model-based analysis. The sponsor’s reported treatment difference and the simple unadjusted recalculation are close in direction and scale, but their confidence limits are not identical. The registry record does not identify the sponsor’s model or explain the precise construction of its interval. No discrepancy flag is recorded. The sponsor’s reported analysis remains the registry-reported result, while the recalculation is useful as a transparent, simple comparison based on posted summary statistics.

What does the secondary analysis estimate?

The LDL-C outcome is reported as least-squares means, with a standard error for each arm, and a treatment difference with a confidence interval. General: a least-squares mean is an estimated group mean from a statistical model; it may account for specified terms in that model. A standard error describes uncertainty in an estimated mean, rather than the spread of individual observations. The model terms and adjustment details are not reported in the registry record, so the least-squares means should be described as reported rather than reconstructed from individual data.

The secondary contrast’s confidence interval includes zero. The registry does not provide a p-value for this analysis. An unadjusted recalculation gives a separate p-value, but it is not a substitute for the sponsor’s analysis or for a multiplicity-adjusted inference. The posted comparison also uses an approximate pooled standard deviation for its planning illustration; this is relevant to those planning calculations, not a claim that individual-level variability was directly available.

Why can binary outcomes require care?

General: a binary outcome reduces each participant’s status to whether a defined event occurred. Risk differences express absolute contrasts in proportions, whereas relative measures such as risk ratios express one group’s risk in relation to another. Different measures can emphasize different aspects of the same data. For uncommon or very common outcomes, estimates may be especially sensitive to a small number of participants changing category. Here, the outcome was common in both arms, and the confidence intervals around the arm percentages and treatment contrast are important for judging precision.

General: over-dispersion matters when the observed variation exceeds what a chosen statistical model expects. In that case, model-based standard errors can be too small if the extra variation is ignored. The registry does not report an over-dispersion assessment or an adjustment, so there is no basis for claiming that one was or was not needed in the sponsor’s analysis.

11. Confidence Intervals and Precision

The primary arm estimates are accompanied by 95% confidence intervals. For AMD, the interval runs from 86.5% to 97.4%; for AI/pen, it runs from 83.4% to 95.8%. These intervals show uncertainty around each arm’s estimated percentage of participants meeting the full-administration definition. They do not describe the range of individual participants’ outcomes.

For the comparison, the recalculated risk-difference interval runs from -0.104 to 0.055. Because it includes zero, the recalculation is compatible with no difference as well as with differences in either direction. The sponsor’s reported interval, from -11.2 to 6.1 percentage points, likewise includes zero. The registry does not report a prespecified margin for equivalence or noninferiority, so these intervals cannot be used to claim that the devices are equivalent or that a meaningful difference has been excluded.

General: precision is about the range of effects compatible with the data under the analysis, not merely whether a test crosses a threshold. A confidence interval can be statistically inconclusive while still excluding some larger effects; whether its limits are sufficiently narrow depends on what differences would matter for the research question. The registry record does not state a threshold for a practically important difference in full administration.

The secondary treatment-difference interval for LDL-C also crosses zero. Its reported limits convey uncertainty about that separate outcome, not uncertainty about the primary administration endpoint. The registry does not report adjusted confidence intervals for multiple outcomes. Overall, the posted intervals support a cautious reading: both arms had high reported completion percentages, while the comparative estimates remain compatible with no difference and with effects in either direction.

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 give participants per arm, not a total sample size or a total number of events. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect: 100%, 75%, or 50%. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 1,789 participants per arm for 80% power and 2,394 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,058 participants per arm for 80% power and 4,093 participants per arm for 90% power. Planning for 50% of the observed effect gives 6,604 participants per arm for 80% power and 8,840 participants per arm for 90% power.

The 80% power column describes the illustrative number of participants per arm under which the assumed effect would be detected at the stated significance level with 80% power, under the listed assumptions. The 90% column uses the corresponding higher power target. Smaller effects need more participants to detect under these assumptions, which is why the planning counts rise as the assumed fraction of the observed effect falls. These calculations use the observed effect as an input and are not observed power.

The secondary outcome has its own planning illustrations, based on its estimated mean difference and the stated approximation. These figures are also participants per arm. They should be read as hypothetical planning scenarios rather than as a recommendation or a claim about the original design. The registry record does not report the trial’s original power target, assumed effect, or sample-size calculation.

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 = 0.939; treatment proportion p₁ = 0.915; average p̄ = 0.927.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3683 = 0.7218.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3679 = 0.3096.
4. n = (0.7218 + 0.3096)² / (-0.0244)² = 1,788.4, rounded up to 1,789 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 <- 0.939024390243902                          # control proportion
p1 <- 0.914634146341463                          # 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(1879319)
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 = 1,789 (80% power), 2,394 (90% power)
 75% of observed effect: n per arm = 3,058 (80% power), 4,093 (90% power)
 50% of observed effect: n per arm = 6,604 (80% power), 8,840 (90% power)
power.prop.test: 1788.4 
Simulated power at n = 1,789 per arm: 0.806 (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 registry analysis reports a treatment difference of -2.4 percentage points for the primary outcome, with a 95% confidence interval from -11.2 to 6.1. The interval includes zero, so the reported result does not establish a statistically clear difference between the device groups. The registry gives no p-value for this analysis and does not identify the statistical method used.

The unadjusted recalculation from posted summary counts estimates a risk difference of -0.024, with a 95% confidence interval from -0.104 to 0.055 and an unadjusted p-value of 0.549. Both estimates point in the same direction, and both intervals include no difference. Their intervals are not identical, which can reflect different analytic approaches or the use of underlying values rather than rounded displayed percentages. The registry record does not explain the sponsor’s method in enough detail to reconcile the interval limits precisely.

The recalculation is a simple comparison from posted summary statistics; it should not be treated as the sponsor’s analysis or as a correction to it. The record does not flag a discrepancy. For the sponsor’s reported conclusion, its own treatment-difference estimate and interval are the direct registry results. The recalculation offers a transparent supplementary view, with its unadjusted nature kept explicit.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and one posted secondary outcome. It does not report a multiplicity strategy, such as a testing hierarchy, adjustment procedure, or allocation of statistical significance across outcomes. When several hypotheses are tested, unadjusted results can overstate the strength of evidence if the collection of tests is treated as a single family. The secondary outcome should therefore be interpreted cautiously, particularly because its registry analysis does not include a reported p-value or multiplicity-adjusted inference.

The primary endpoint is defined as full administration at both Weeks 4 and 8, with telephone interviews assessing whether attempted injections were given fully, partially, or not at all. Only full administrations inside the prespecified visit window were included. The registry does not report the number of missing interviews, how missing responses were handled, whether participants with an unavailable visit were counted as not meeting the endpoint, or whether sensitivity analyses were conducted. These details matter because missing reports could affect the estimated percentage if missingness is related to administration success.

The primary population is named as the full analysis set, but the registry record does not give further criteria for membership in that set or explain how participants without an evaluable endpoint were handled. It lists 82 participants in each arm for the posted primary results. That information alone does not establish whether every enrolled participant contributed complete data at both visits.

The registry identifies the study as randomized and unmasked, but does not report sequence-generation or allocation-concealment details. The sponsor’s statistical method for the primary analysis is also not stated. These omissions do not invalidate the posted result, but they limit assessment of how the reported interval was constructed and whether missing data, covariates, or other design features were addressed. The registry does not report interim analyses or a detailed statistical analysis plan.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: deep vein thrombosis (1.2%).

The registry lists serious adverse events for the two arms. In the AMD arm, 0 serious adverse events were reported among 82 participants at risk. In the AI/pen arm, 1 serious adverse event was reported among 82 participants at risk. The registry identifies deep vein thrombosis as the top serious-event term, at 1.2%. These figures describe the posted serious-event records and do not, by themselves, establish that an event was caused by the study treatment or the device.

The registry reports 0 other adverse events in each arm. Death counts are not reported in the registry record. The record does not provide additional detail in these fields about event timing, severity beyond the serious-event classification, or a causal assessment. Because the study focused on administration and had a short treatment period, the safety counts should be read as descriptive observations from this trial, not as a comprehensive comparison of longer-term safety.

Small numbers of serious events make comparative interpretation especially uncertain. The posted counts should not be converted into a claim that one device is safer. Safety results also do not answer the primary question about full administration at both home-use visits.

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

The primary results show that a high percentage of participants in each arm were reported to have fully administered evolocumab at both Weeks 4 and 8, using the registry’s telephone-interview definition and visit-window rule. The estimated difference between the groups is small in the posted analyses, and the sponsor-reported and recalculated confidence intervals both include no difference. The data therefore do not establish a statistically clear difference in the primary endpoint.

This is not the same as demonstrating equivalence. An equivalence conclusion requires a prespecified margin defining how much difference would be acceptable and an analysis showing that the uncertainty lies within that margin. The registry does not report such a margin. Nor does the absence of a clear difference establish that the devices are interchangeable for every user or every setting.

The result is specific to the enrolled population, the study’s device procedures, the measured visits, and the outcome definition. It concerns full administration at both specified home-use visits, as reported in telephone interviews. It does not establish sustained use after the study period, successful use without the supervised clinic administration, or performance in populations not represented by this trial. Further details about interview verification and handling of missing reports are not reported in the registry record.

The secondary LDL-C result is separate: both groups had reductions from baseline, and the comparative interval includes no difference. It does not determine whether participants completed the administration task and does not substitute for the primary endpoint. Likewise, the serious-adverse-event counts are descriptive and too limited to support a broad comparative safety conclusion.

Overall, the posted results support a bounded interpretation: participants in both groups commonly met the stated full-administration criterion, while the comparative estimates remain uncertain. They do not establish equivalence, a clinically important advantage for either method, or results beyond the outcomes and follow-up recorded in this study.

18. Why This Trial Matters Statistically

This study asks a practical statistical question: whether participants can complete a defined administration task using one of two devices in a home-use setting. The comparison is informative because the outcome is tied to a specific behavior—full administration at both Weeks 4 and 8—rather than relying only on a general impression of device usability. A clear endpoint definition makes the meaning of the reported percentages easier to understand.

The analysis also illustrates why a comparison requires more than looking at the two arm percentages. Both percentages are high, but the relevant comparative estimate is the difference between them, together with its uncertainty. The confidence intervals show that the observed data do not pin down a single precise contrast. Reporting uncertainty prevents a small numerical separation from being mistaken for firm evidence of a device advantage.

The registry results also distinguish sponsor analysis from a transparent unadjusted recalculation. The two approaches produce similar directional readings, but the registry does not document the sponsor’s method. This makes it important to identify which estimate is reported by the sponsor and which is a simple recalculation, rather than blending them into one result.

Finally, the study shows the limits of a binary endpoint and a short assessment period. A full-versus-not-full classification summarizes completion, but does not describe partial administration, reasons for difficulty, or continued use beyond the specified visits. Recognizing those limits is part of sound statistical interpretation: the endpoint can inform the study’s stated usability question without being stretched into claims about longer-term treatment outcomes or broad device equivalence.

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 registry record leaves several trial-specific details unclear. The arm descriptions are truncated after describing home administration, so the complete home-use procedures and any associated support are not reported. The record does not detail how randomization was generated, whether allocation was concealed, or how telephone interview reports were verified. Since the primary outcome depends on self-report, independent verification is not documented.

The endpoint includes only full administrations within the prespecified visit window. The registry does not report the number or handling of missed interviews, out-of-window administrations, partial injections, or other unavailable outcome data. It also does not give further criteria for the full analysis set. These omissions make it harder to assess the potential effect of missing or excluded information on the primary estimate.

The sponsor’s method for the primary treatment difference is not identified, and the registry does not explain the construction of its confidence interval. Details of the model behind the secondary least-squares means are also not reported. No multiplicity strategy, interim-analysis information, or original sample-size justification is reported in the registry record.

The assessment period was described as 8 weeks, and the primary outcome focuses on Weeks 4 and 8. The results therefore do not describe longer-term use. The record also does not provide a prespecified margin for equivalence or noninferiority, limiting conclusions about whether the devices perform similarly within an acceptable range. These limitations shape interpretation of this trial’s posted results but do not erase the descriptive evidence that full administration was commonly reported in both arms.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess in Home Use of Evolocumab (AMG 145) Administration Using Either an Automated Mini-doser or a Prefilled Autoinjector/Pen — NCT01879319.
• Registry record last updated 2022-11-30; status last verified 2022-11.
• Results first posted 2015-12-23.
• 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

NCT01879319 is a completed, randomized, unmasked, parallel-group Phase 3 study sponsored by Amgen. It enrolled participants with primary hypercholesterolemia or mixed dyslipidemia to compare home-use administration of evolocumab with an automated mini-doser or a prefilled autoinjector/pen.

The primary endpoint was the percentage of participants with full administration at both Weeks 4 and 8, based on telephone interviews and restricted to full administrations inside the prespecified visit window. The registry reports high percentages in both arms, while the sponsor’s treatment-difference interval includes no difference. An unadjusted recalculation leads to the same broad interpretation but is not a substitute for the sponsor’s analysis.

The posted secondary outcome assessed LDL-C change at the mean of Weeks 10 and 12; its comparative interval also includes no difference. The registry does not report a multiplicity plan, detailed missing-data handling, or the sponsor’s statistical methods. Overall, the record supports a descriptive account of administration success in both groups, with uncertainty about the comparative effect and limits on claims of equivalence or longer-term use.