Study to Assess In-home Use of Evolocumab (AMG 145) Using a Prefilled Syringe 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) Using a Prefilled Syringe or a Prefilled Autoinjector/Pen (NCT01849497), a randomized phase 3 study. The primary outcome is Percentage of Participants With Full Administration of Evolocumab at Both Weeks 2 and 4.

2. Clinical Question

The central question is whether participants with primary hypercholesterolemia or mixed dyslipidemia can administer a full dose of evolocumab at home with either of two delivery devices. The registry compares a prefilled syringe with a prefilled autoinjector/pen. The primary outcome concerns full administration at both home-use visits, Weeks 2 and 4, rather than a comparison of cholesterol outcomes.

The question is about participants’ ability to use the assigned device in a home setting over the scheduled administrations. It does not directly test whether one device changes cholesterol more than the other, nor does it establish a general preference between devices. The registry also reports a secondary LDL-C outcome, which addresses a different aspect of the comparison.

3. Trial Design

This was a completed Phase 3, randomized, parallel-group study sponsored by Amgen. The registry lists enrollment of 149 participants and describes the study as multicenter. Masking is listed as none. The study began on 2013-04-18, and primary completion was 2013-09-02.

Participants were assigned to use either evolocumab with a prefilled syringe or evolocumab with a prefilled autoinjector/pen. Both groups followed the same schedule: 140 mg every 2 weeks for 4 weeks, by subcutaneous administration on Day 1, Week 2, and Week 4. The first administration was self-administered in the clinic under supervision; the subsequent administrations were self-administered at home. The recorded group sizes for the primary outcome are 75 for the syringe group and 74 for the autoinjector/pen group.

The primary outcome was the percentage of participants with full administration at both Weeks 2 and 4, assessed by telephone interview. The registry also lists percent change from baseline in LDL-C at Week 6 as a secondary outcome. These outcomes differ in kind: one records reported device use at two home visits, while the other measures a laboratory-based change over time.

The registry record does not report the sequence-generation procedure, allocation-concealment method, or further details of masking beyond none. The original sample-size justification, planned statistical analysis details, and whether interim analyses were planned are not reported in the registry record. The available design description therefore supports a basic account of the randomized comparison and schedule, but not reconstruction of every design or analysis decision.

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 2 and 4, measured over Week 2 and Week 4.

The primary endpoint is the percentage of participants who achieved full administration of evolocumab at both Week 2 and Week 4. A telephone interview asked about all attempted injections and whether an injection was administered in part, in full, or not at all. To meet this endpoint, a participant had to report full administration at each of the two home-use visits; the outcome is therefore a participant-level binary classification based on the reports from both visits.

This endpoint was chosen to address the study’s stated objective: assessing users’ ability to administer a full dose at home with either device. It focuses on completion of the intended administration, not on the participant’s preference, ease-of-use rating, or the amount of LDL-C change. The registry identifies the analysis population as the full analysis set.

Because the outcome is based on telephone interviews, it represents reported administration rather than an independently described measurement of the delivered dose. The registry record does not report further details about interview procedures, confirmation of administration, or how incomplete or unavailable interview information was handled. Those details matter when interpreting a self-reported endpoint, because outcome classification depends on the information collected at each scheduled home-use visit.

7. Results Posted in the Registry

• Evolocumab AI/Pen: 89.2% (66/74) versus 96.0% (72/75) on control; risk difference -6.8 percentage points (95% CI -15.2 to 1.5), risk ratio 0.93 (0.85–1.02); unadjusted two-proportion z-test p = 0.112.

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 Week 6

• 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 -63.43 versus -59.74 on control; difference -3.69 (95% CI -10.95 to 3.57), standardized effect d = -0.16; z-test p = 0.319.
• 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 lists one secondary endpoint: percent change from baseline in LDL-C at Week 6. Its estimates indicate reductions from baseline in both groups, with a numerically larger reduction in the autoinjector/pen group. The estimated between-group difference has an interval that includes zero, so the secondary comparison does not provide a clear separation between devices on this measure. The specific estimates and intervals are reported with the endpoint results; the interpretation should remain distinct from the primary home-administration outcome.

The two outcomes address different questions. Full administration at both home visits concerns reported use of the assigned device. LDL-C change concerns a measured clinical biomarker over the follow-up described. A result on one endpoint does not validate, explain, or replace the other. The secondary result can add context about the study’s measured outcomes, but it is not a direct test of whether participants can complete home administration.

Secondary results generally carry less confirmatory weight when multiple outcomes or comparisons may be examined and no adjustment strategy is reported. Considering multiple results can increase the chance that at least one appears notable by chance. The registry record does not report whether multiplicity was addressed, whether the LDL-C outcome was designated for confirmatory testing, or what hierarchy governed interpretation. Its unadjusted recalculation should therefore be viewed as exploratory context rather than as an independent confirmation of the primary finding.

The registry reports one secondary outcome, but the number of analyses and the full statistical plan do not establish how the sponsor intended to control the overall interpretation across outcomes. Without those details, the secondary result is best read descriptively and with appropriate caution, rather than treated as decisive evidence about either device.

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

• Percent Change From Baseline in LDL-C at Week 6

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the definition of full administration at both home-use visits or did not. For a binary outcome, a percentage describes the share of participants meeting the endpoint. A comparison between groups can be expressed as a difference in those shares, with the sign indicating which group has the higher observed proportion according to the comparison’s coding.

What does a confidence interval describe?

In general, a confidence interval describes the uncertainty around an estimate under the statistical method used. A wider interval indicates less precision than a narrower interval. For a difference between groups, an interval that includes zero is compatible with no difference under that method, while values on either side of zero represent different possible directions and magnitudes of difference. An interval is not a guarantee that the true value lies within its bounds, nor does it identify which value is most likely without additional assumptions.

The registry gives group percentages with 95% confidence intervals and also gives a treatment-difference estimate with its own 95% interval. The group intervals and the interval for the difference answer related but distinct questions. The first describe uncertainty in each group’s endpoint percentage; the second describes uncertainty in the contrast between groups. Interpreting a treatment comparison requires attention to that contrast, rather than relying only on whether the separate group intervals overlap.

How should the unadjusted comparison be read?

The recalculation uses posted summary counts to estimate an unadjusted risk difference and its interval. It does not reproduce an adjusted model or any unreported details of the sponsor’s statistical procedure. The unadjusted p-value is a summary of how compatible the observed data are with a specified no-difference calculation under its assumptions. It is not the probability that the no-difference hypothesis is true, and it does not state the probability that the observed difference arose by chance.

Because the primary endpoint is binary, the comparison is based on counts of participants who met the endpoint and the total number assessed in each group. Binary outcomes can be summarized in more than one way, including risk differences, risk ratios, or odds ratios. These measures use different scales and need not have the same numerical value or interpretation. The registry’s reported treatment difference and the recalculated risk difference should therefore be understood according to their stated scales, not treated as interchangeable numbers.

Why does the endpoint definition matter?

The endpoint requires full administration at both Week 2 and Week 4. It is not the percentage who completed a single injection, nor the percentage who completed at least one of the two home injections. The telephone interview asked about attempted injections and classified administration as partial, full, or none. The registry does not report more detailed rules for combining responses across visits or handling missing interview information. The exact operational handling of those cases is therefore not reported in the registry record.

The endpoint also depends on participants’ reports. In general, self-report can capture what participants experienced at home, but it may differ from a directly observed administration assessment. The registry description identifies telephone interviews as the assessment method but does not provide enough detail to evaluate how reporting was checked or whether interviewers were masked. Masking is listed as none for the study.

How should the LDL-C result be distinguished?

The secondary endpoint is percent change from baseline in LDL-C at Week 6. It is summarized as a least-squares mean with a standard error in each group, and a mean difference is reported for the comparison. These are continuous-outcome summaries, unlike the primary endpoint’s percentages. A mean describes the average change under the stated analysis, while a standard error describes precision of an estimated mean; it is not the same quantity as the spread of individual participant results.

The unadjusted recalculation for this secondary comparison is based on the posted summary statistics, with an approximate pooled standard deviation noted in the calculations. It should not be mistaken for a reconstruction of an unpublished model or for the sponsor’s full analysis. The registry record does not report the model details for the least-squares means, the covariates used, or other implementation choices.

What remains unknown about the analysis?

The registry record does not report the original sample-size justification, a full statistical analysis plan, or whether interim analyses were planned. It also does not report details of missing-data handling, multiplicity adjustment, or a method for adjusting the primary comparison. Those unknowns should not be filled in by assuming conventional choices. The planning illustrations are based on the observed effects and stated assumptions; they are not evidence about the trial’s original design target or its actual power.

11. Confidence Intervals and Precision

The primary group estimates are 96.0% for the prefilled-syringe group, with a 95% confidence interval from 88.9% to 98.6%, and 89.2% for the autoinjector/pen group, with a 95% confidence interval from 80.1% to 94.4%. These intervals convey uncertainty about each group’s percentage. They are not ranges containing every participant’s outcome, and they do not indicate that the percentage is equally plausible at every point in the interval.

For the between-group comparison, the unadjusted recalculated risk difference is -0.068, with a 95% confidence interval from -0.152 to 0.015. The interval includes zero, so the data do not rule out no difference under this calculation. It also extends to values on either side of zero, meaning the direction of the underlying difference is not settled by this interval. The interval’s width is important: the estimate is not precise enough to restrict the plausible contrast to a narrow range around the point estimate.

Confidence intervals should be interpreted together with the endpoint and analysis method. They do not resolve whether any possible difference would be important in practice, because the registry record does not report a threshold for an important difference. Nor do they prove equivalence. That conclusion would require a prespecified margin and an analysis designed to assess it, which are not reported in the registry record.

The registry also reports a sponsor treatment-difference interval, described separately in the sponsor analysis. Because the reported and recalculated intervals are based on different analysis presentations, they should not be silently combined. The posted estimates are most informative when each is read with its stated method and scale.

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 for this two-group comparison; they are not total event counts. Each effect row considers planning for 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. The columns for 80% and 90% power indicate the number of participants per arm that would be planned, under the stated assumptions, to have the corresponding probability of detecting the specified effect if that effect were the true one and the model assumptions held.

The stated 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 the stated fraction of the observed effect. These are planning assumptions for the illustration, not the trial’s original design assumptions. The original sample-size justification and design assumptions are not reported in the registry record.

Power is the long-run probability of detecting an effect of a specified size under a defined design and analysis, if that effect exists and the assumptions are appropriate. The 90% column represents a higher target probability of detection than the 80% column, and it therefore calls for more participants under the same planning setup. Planning for a smaller effect also requires more participants, because a smaller contrast is harder to distinguish from random variation.

These figures are not observed power. They are forward-looking planning illustrations calculated from the observed effect, not a measurement of how much power the completed trial achieved. They should not be used to infer that the trial was designed for these sample sizes, since the registry record does not report its original sample-size rationale.

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 = 0.960; treatment proportion p₁ = 0.892; average p̄ = 0.926.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3703 = 0.7258.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3672 = 0.3090.
4. n = (0.7258 + 0.3090)² / (-0.0681)² = 230.9, rounded up to 231 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 <- 0.96                          # control proportion
p1 <- 0.891891891891892                          # 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(1849497)
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 = 231 (80% power), 309 (90% power)
 75% of observed effect: n per arm = 368 (80% power), 492 (90% power)
 50% of observed effect: n per arm = 727 (80% power), 973 (90% power)
power.prop.test: 230.9 
Simulated power at n = 231 per arm: 0.808 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary comparison as a treatment difference of -6.8, with a 95% confidence interval from -16.3 to 2.0. No p-value or analysis method is specified for that reported analysis in the registry record. The sponsor estimate is the registry’s own reported comparison and should be distinguished from the unadjusted recalculation based on the posted group counts.

The recalculation expresses the contrast as a risk difference of -0.068, with a 95% confidence interval from -0.152 to 0.015, and an unadjusted p-value of 0.112. The registry’s reported estimate and interval use a different numerical presentation from the recalculated values. They are both comparisons of the device groups, but the registry record does not report enough method detail to explain the precise source of the difference between the intervals. The discrepancy flag is false, so the available information does not identify a discrepancy requiring the sponsor result to override the recalculation.

Neither presentation supports a definitive claim that the devices differ on the primary endpoint: the reported interval and recalculated interval both include zero on their respective scales. The sponsor analysis should be read as the registry-reported result, while the recalculation is a supplementary unadjusted analysis of posted summary statistics. It cannot substitute for unavailable details of the sponsor’s analysis plan or model.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one endpoint, comparison, time point, or analysis. In general, the more opportunities there are to identify an apparently notable result, the more important it becomes to specify in advance how the overall error rate will be handled. Possible strategies include a prespecified testing hierarchy or adjustment procedures, but the registry record does not report whether any such strategy was used. No particular approach should be assumed.

The registry identifies a primary endpoint and one secondary endpoint. It also reports a primary comparison and a secondary comparison. The primary endpoint is the main measure of home-use administration; the secondary endpoint is LDL-C change at Week 6. The registry record does not report the full statistical analysis plan, the intended relationship between the endpoints, or whether the secondary endpoint was intended for confirmatory inference. The unadjusted recalculations do not account for multiplicity.

The primary analysis population is identified as the full analysis set. The registry record does not provide further details about the definition of that set, exclusions from it, or whether all randomized participants contributed to each outcome. It also does not report how missing interviews or missing LDL-C measurements were handled, whether any imputation was used, or whether sensitivity analyses were performed. Those omissions matter because missing outcomes can affect both the estimated percentages and the comparison, particularly when the outcome depends on responses collected at multiple visits.

The registry’s description of telephone interviews gives the general basis for primary endpoint classification, but not the rules used for incomplete records or participants who could not be reached. The posted results should therefore be interpreted as the results reported for the stated analysis population, without assuming that missingness was absent or handled in a particular way.

The record does not report whether interim analyses were planned or conducted, nor does it report the trial’s original sample-size justification. Those design and analysis details cannot be inferred from the sample-size planning illustrations, which are based on the observed effects and explicit planning assumptions rather than on the original protocol.

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebrovascular accident (1.4%), glomerulonephritis minimal lesion (1.4%), gastrooesophageal reflux disease (1.3%), cholecystitis (1.3%), cholelithiasis (1.3%).

The registry reports serious adverse event counts of 3 among 75 participants at risk in the prefilled-syringe group and 2 among 74 participants at risk in the autoinjector/pen group. It also reports other adverse event counts of 4 among 75 and 2 among 74, respectively. These are descriptive counts from the registry and should not be interpreted as proof that an event was caused by the assigned treatment or that one device is safer than the other.

The registry also lists serious-event terms with percentages, including cerebrovascular accident at 1.4%, glomerulonephritis minimal lesion at 1.4%, gastrooesophageal reflux disease at 1.3%, cholecystitis at 1.3%, cholelithiasis at 1.3%, and asthma at 1.3%. The available record does not specify arm-specific attribution for these listed terms in the information, so they should not be assigned to a particular group. Deaths are not reported in the registry record.

Adverse-event counts are not a substitute for a comparative safety analysis. The registry information does not provide event timing, severity beyond the serious classification, attribution, or a statistical comparison. The small group sizes and the study’s short administration schedule also mean that the counts are descriptive of this trial rather than a comprehensive account of longer-term safety.

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

The primary result describes reported full administration at both home-use visits in participants assigned to one of the two evolocumab delivery devices. It shows high observed percentages in both groups, with a numerical difference favoring the prefilled-syringe group on the endpoint as defined. The uncertainty around the comparison includes no difference, so the posted data do not establish a definitive between-device difference.

This finding is not proof that the devices are equivalent. Equivalence requires a prespecified acceptable range for differences and an analysis designed to test that question. Such a margin and analysis are not reported in the registry record. Likewise, the result does not establish that either device is better or worse for all users or in settings beyond the study’s conditions.

The endpoint is narrowly defined: full administration at both Week 2 and Week 4, based on telephone interviews about attempted injections. It does not measure usability in every respect, long-term persistence, patient preference, or performance under a different schedule. The registry’s LDL-C outcome is a separate secondary measure and should not be conflated with successful administration.

The study was randomized and compared parallel groups, but masking is listed as none. The reported outcome is self-reported by telephone, and the registry does not provide detail on confirmation procedures or missing-data handling. These features are relevant when judging how strongly the percentages represent actual administration and how robust the comparison is.

The results also do not support medical advice. They describe what was observed in this particular study, with its participants, devices, follow-up schedule, and available registry reporting. Broader conclusions would require evidence that addresses other populations, longer-term use, and outcomes beyond the short home-use assessment.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary endpoint is closely tied to the practical task under study: completing full-dose self-administration at home on two scheduled occasions. The outcome is a participant-level percentage, which makes the comparison straightforward to describe, but the contrast remains uncertain even when the group percentages are high. The interval for the difference is more useful for judging that uncertainty than the point estimates alone.

The study also illustrates why a non-significant or uncertain comparison is not the same as proof of equivalence. The posted interval includes zero, but the registry does not report a margin defining what differences would be acceptable. Without such a margin and a suitable design, the analysis cannot establish that the devices perform alike within a clinically acceptable range.

Its dual outcome structure also illustrates the distinction between an operational endpoint and a biomarker endpoint. Reported completion of home administration and change in LDL-C answer separate questions. The latter can add context, but it cannot substitute for the primary assessment of device use. The absence of reported multiplicity procedures makes it especially important not to overstate secondary findings.

Finally, the planning illustrations demonstrate how assumed effect size affects sample-size requirements. They are based on the observed effect and stated assumptions, not the original trial design or observed power. Keeping those planning calculations separate from the completed study’s outcome results helps prevent retrospective planning figures from being mistaken for evidence about the trial’s design adequacy.

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 endpoint relies on telephone interviews about attempted injections. This approach captures reported home-use experience, but the registry record does not describe independent confirmation of full administration, interviewer procedures, or methods for resolving uncertain responses. The outcome also requires full administration at both home visits, and the record does not describe how missing information at either visit was handled.

The follow-up described for device administration is brief: the scheduled administrations span 4 weeks, with the primary endpoint assessed at Weeks 2 and 4. The findings therefore address the stated short-term home-use task, not continued use over a longer period. The registry does not report participant preferences, usability ratings, or detailed demographic and clinical characteristics in the information summarized for this trial, limiting assessment of how the results may vary across types of users.

Masking is listed as none. The registry record does not report whether outcome interviewers were masked or provide further information about allocation concealment. It also does not report missing-data procedures, a complete statistical analysis plan, multiplicity handling, or an equivalence margin. These gaps limit reconstruction of the analysis and the strength of claims that can be made from the reported comparison.

The secondary LDL-C endpoint addresses a different question and is not a substitute for the primary administration outcome. The registry reports one secondary result, but does not report a multiplicity strategy or enough model details to reproduce the sponsor’s analysis. Adverse-event information is also summarized descriptively, without the timing, attribution, or detailed comparative analysis needed for broader safety conclusions.

Finally, the sample-size illustrations use the observed effect as a planning basis and do not reveal the original design rationale. They cannot resolve whether the trial was planned to assess a particular degree of difference or equivalence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess In-home Use of Evolocumab (AMG 145) Using a Prefilled Syringe or a Prefilled Autoinjector/Pen — NCT01849497.
• Registry record last updated 2018-11-29; status last verified 2018-11.
• Results first posted 2015-10-09.
• 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

NCT01849497 is a completed Phase 3 randomized, parallel-group study sponsored by Amgen. It enrolled 149 participants with primary hypercholesterolemia or mixed dyslipidemia and compared evolocumab delivered by prefilled syringe with evolocumab delivered by prefilled autoinjector/pen. Masking is listed as none.

Both groups followed a schedule of 140 mg every 2 weeks for 4 weeks. Participants self-administered under supervision in the clinic on Day 1 and at home at Weeks 2 and 4. The primary endpoint was the percentage with full administration at both home visits, assessed by telephone interview. The registry also reports percent change from baseline in LDL-C at Week 6 as a secondary endpoint.

The observed primary percentages were high in both groups, while the between-group uncertainty interval includes zero. The registry record does not report the original sample-size justification, full statistical analysis plan, missing-data handling, or multiplicity procedures. The results are best understood as estimates of short-term, reported home-use administration in this randomized comparison.