PREventative Study Against URate-lowering Drug-induced Gout Exacerbations 1: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PREventative Study Against URate-lowering Drug-induced Gout Exacerbations 1 (NCT00829829), a randomized phase 3 study. The primary outcome is Number of Gout Flares Per Participant Assessed From Day 1 to Day 112 (Week 16).

2. Clinical Question

The clinical question is about flare frequency during the period of allopurinol initiation, rather than only whether a participant experienced any flare. A participant could contribute more than one flare to the primary measure. The registry’s flare definition required acute articular pain typical of a gout attack that required anti-inflammatory treatment, with at least 3 of 4 specified joint signs or symptoms and at least 1 additional feature, such as rapid onset of pain or joint warmth.

The trial also registered outcomes concerning modified gout flares, whether participants experienced one or more or two or more flares, and days with flares, including days with a pain score of 5 or more. Those outcomes broaden the description of flare burden, but they do not change the primary question: whether the average number of defined flares differed between each rilonacept group and placebo over the stated follow-up period. The registry record does not report the trial’s original sample-size justification or a prespecified statistical analysis plan.

3. Trial Design

This was a Phase 3, randomized, parallel-group, placebo-controlled study sponsored by Regeneron Pharmaceuticals. The registry records enrollment of 241 participants, a start date of 2009-02, primary completion in 2010-05, and a completed status. The stated purpose was to assess the safety and effectiveness of rilonacept for preventing gout flares in participants starting allopurinol therapy. The registry describes the study as double-blind and quadruple-masked.

Three groups were registered: placebo, rilonacept 80 mg, and rilonacept 160 mg. Each regimen began with two subcutaneous injections on Day 1, followed by one injection weekly from Week 1 to Week 15. For the 80 mg group, the Day 1 loading dose was a total of 160 mg; for the 160 mg group, it was a total of 320 mg. The placebo group received matching placebo injections according to the listed schedule.

The primary measure covered Day 1 to Day 112 (Week 16). The primary outcome results use 79 participants in the placebo group, 80 in the 80 mg group, and 80 in the 160 mg group. The primary population is described as randomized participants who received any study medication, analyzed according to treatment allocated at randomization. For participants who dropped out, only flares occurring before Day 112 were counted, regardless of whether they occurred during the treatment period.

The registry record lists six outcome measures and five secondary outcomes, but it does not report a detailed account of allocation procedures, the original sample-size rationale, interim monitoring, or a full statistical analysis plan. Those features should not be inferred from the general design labels. The record also contains no reported analysis entries, so the available comparisons should be read as the posted summary results and unadjusted comparisons, not as a complete account of every analysis performed by the sponsor.

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: Out of 468 participants, 241 were randomized and 240 treated in the study. Participants were randomized in 1:1:1 ratio to receive either Placebo or Rilonacept 80 mg or Rilonacept 160 mg.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) that included all randomized participants who received any study medication and was based on the treatment allocated by IIVRS at randomization (as randomized).

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: Baseline population included full analysis set (FAS) comprising of all randomized participants who received any study medication and was based on treatment allocated by Interactive voice response system (IVRS) at randomization (as randomized).

6. Primary Endpoint

The registry lists the primary outcome as Number of Gout Flares Per Participant Assessed From Day 1 to Day 112 (Week 16), measured over Day 1 to Day 112 (Week 16).

The primary endpoint is the number of gout flares per participant from Day 1 to Day 112 (Week 16), reported as a mean with a standard deviation for each group. It measures the frequency of defined flares over a fixed period. Unlike a yes-or-no endpoint for at least one flare, a count measure can distinguish participants with multiple flares from those with only one, and it can include participants with no flare.

The registry defines a flare as participant-reported acute articular pain typical of a gout attack that required treatment with an anti-inflammatory therapeutic. The definition also required at least 3 of 4 signs or symptoms—joint swelling, tenderness, redness, and pain—and at least 1 of rapid onset of pain, decreased range of motion, joint warmth, or other symptoms similar to a prior gout flare. This operational definition specifies which episodes contribute to the count; it does not imply that every episode of joint pain would qualify.

For the primary outcome, the placebo group mean was 1.06 flares per participant (standard deviation 1.59). The corresponding means were 0.29 (standard deviation 0.77) for rilonacept 80 mg and 0.21 (standard deviation 0.54) for rilonacept 160 mg. These summaries describe average counts and variation within each group during the stated follow-up. The registry states that participants who dropped out contributed only flares occurring before Day 112, whether or not those flares occurred during treatment.

A mean count is useful for summarizing total flare burden across a group, but it can conceal differences in how counts are distributed among participants. The registry record does not report the distribution of individual counts or a model specifically accounting for count-data features. The endpoint therefore supports a comparison of posted group averages, while leaving other aspects of the flare pattern less fully characterized.

7. Results Posted in the Registry

• Rilonacept 80 mg: mean 0.29 versus 1.06 on control; difference -0.77 (95% CI -1.16 to -0.38), standardized effect d = -0.62; z-test p = <0.001.
• Rilonacept 160 mg: mean 0.21 versus 1.06 on control; difference -0.85 (95% CI -1.22 to -0.48), standardized effect d = -0.72; z-test p = <0.001.

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.

Number of Modified Gout Flares Per Participant From Day 1 to Day 112 (Week 16)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Rilonacept 80 mg: mean 0.40 versus 1.19 on control; difference -0.79 (95% CI -1.22 to -0.36), standardized effect d = -0.57; z-test p = <0.001.
  • Rilonacept 160 mg: mean 0.28 versus 1.19 on control; difference -0.91 (95% CI -1.32 to -0.50), standardized effect d = -0.69; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Rilonacept 80 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Rilonacept 160 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With at Least One Gout Flare From Day 1 to Day 112 (Week 16)

• 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:
  • Rilonacept 80 mg: 18.8% (15/80) versus 46.8% (37/79) on control; risk difference -28.1 percentage points (95% CI -42.0 to -14.1), risk ratio 0.40 (0.24–0.67); unadjusted two-proportion z-test p = <0.001.
  • Rilonacept 160 mg: 16.0% (13/81) versus 46.8% (37/79) on control; risk difference -30.8 percentage points (95% CI -44.4 to -17.2), risk ratio 0.34 (0.20–0.59); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rilonacept 80 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rilonacept 160 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With at Least Two Gout Flares From Day 1 to Day 112 (Week 16)

• 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:
  • Rilonacept 80 mg: 5.0% (4/80) versus 31.6% (25/79) on control; risk difference -26.6 percentage points (95% CI -38.0 to -15.3), risk ratio 0.16 (0.06–0.43); unadjusted two-proportion z-test p = <0.001.
  • Rilonacept 160 mg: 3.7% (3/81) versus 31.6% (25/79) on control; risk difference -27.9 percentage points (95% CI -39.0 to -16.9), risk ratio 0.12 (0.04–0.37); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rilonacept 80 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rilonacept 160 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The reported secondary outcomes follow a pattern consistent with the primary endpoint’s direction: the posted group summaries show lower flare burden in both rilonacept groups than in placebo for modified flare counts and for the proportions experiencing at least one or at least two flares. These outcomes describe related but distinct aspects of flare experience. Count outcomes capture repeated events, while threshold outcomes distinguish whether participants crossed a defined event count.

This consistency adds context to the primary result because it suggests that the group-level pattern is not confined to a single way of summarizing flares. It does not make the outcomes independent confirmations: the measures concern overlapping events in the same study population and follow-up period. A participant’s flare count can contribute to more than one of these summaries, so agreement across them should not be treated as replication in a separate sample.

The registry also lists the number of gout flare days per participant and the number of flare days with a participant pain score of 5 or more. Results for those two outcomes are not reported in the registry record. Their absence means the available secondary results do not provide a complete description of duration or higher-pain flare days.

The posted secondary comparisons are unadjusted, and the registry record contains no reported analysis entries. Multiple outcomes and dose comparisons create a multiplicity concern: even if each individual test uses a conventional threshold, considering many tests raises the chance that some results appear statistically notable by chance. Without a reported adjustment or testing hierarchy, secondary p-values carry less evidential weight than a single prespecified primary comparison would. The secondary results are best read as supportive descriptive context, not as a separate basis for a definitive claim.

The secondary pattern is informative about how the registered outcomes align, but it does not resolve the limitations in analysis reporting. In particular, the record does not state how secondary testing was prioritized, whether any outcomes were treated as confirmatory, or how incomplete diary information was handled. Interpretation should remain tied to the outcomes with posted values and their unadjusted status.

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

• Number of Modified Gout Flares Per Participant From Day 1 to Day 112 (Week 16)
• Percentage of Participants With at Least One Gout Flare From Day 1 to Day 112 (Week 16)
• Percentage of Participants With at Least Two Gout Flares From Day 1 to Day 112 (Week 16)
• Number of Gout Flare Days Per Participant From Day 1 to Day 112 (Week 16)
• Number of Gout Flare Days With Participant's Pain Score of 5 or More (From Daily Diary) Per Participant From Day 1 to Day 112 (Week 16)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count summarized as a mean and standard deviation. A mean is the arithmetic average of participant-level flare counts; a standard deviation describes how much those counts typically vary around the average. These two quantities answer different questions. The mean describes average burden, while the standard deviation reflects dispersion. Neither alone shows the full distribution, such as whether counts are concentrated at zero or whether a small number of participants have unusually high counts.

What does the mean difference represent?

The posted mean difference compares the average count in one rilonacept group with the average count in placebo. A negative difference means the posted mean is lower in the rilonacept group under the subtraction convention used for the comparison. For rilonacept 80 mg, the reported difference was -0.77 flares per participant; for rilonacept 160 mg, it was -0.85. These are unadjusted comparisons, and the registry record does not report covariate-adjusted estimates.

A mean difference keeps the result on the endpoint’s original scale: flares per participant over the specified follow-up. This makes the estimate directly interpretable alongside the group means. It is not a relative measure, and it should not be confused with a percentage change or a risk difference. The registry reports separate comparisons of each active group with placebo, not a direct comparison between the active groups.

How should the p-values be read?

A p-value describes how unusual data at least as discrepant as the observed data would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The posted unadjusted values are p < 0.001 for each primary comparison. Because the registry record does not include a complete analysis plan or analysis entries, the precise test and model used by the sponsor are not reported in the registry record. The displayed p-values should therefore be understood as the posted unadjusted comparisons, not as evidence that every modeling choice is documented.

General statistical context: p-values are sensitive to sample size and variability as well as to the magnitude of a difference. A small p-value can coexist with uncertainty about the size of the effect, which is why the estimated difference and its confidence interval are also important. Conversely, a p-value alone does not describe the range of effect sizes that remain compatible with the data.

Why can count outcomes need special care?

General statistical context: count outcomes are nonnegative and may have distributions unlike a continuous measurement that is approximately symmetric. Counts may be concentrated at zero, may be skewed, or may vary more than a simple model expects. Over-dispersion means that the observed variation exceeds what a model’s assumed distribution allows. If that occurs and the model does not account for it, estimated uncertainty and statistical tests can be unreliable. These are general considerations for count data, not claims about the distribution in this trial. The registry reports means and standard deviations but does not report a count model, distributional checks, or a detailed justification for the analysis scale.

The use of a mean difference can still be informative because it summarizes average counts in the original units. But a more complete statistical account could describe the individual count distribution and explain how the analysis addressed zeros, skewness, repeated events, or unequal observation time. Such details are not reported in the registry record. The stated dropout rule counts flares only through the date of dropout for participants who leave before Day 112; the record does not describe an imputation procedure for the unobserved period after dropout.

What does a confidence interval add?

A confidence interval is an interval estimate expressing uncertainty about an underlying group difference under the method’s assumptions. It provides a range of values compatible with the observed data and model, rather than only a single estimate. For both primary comparisons, the reported intervals are entirely below zero. The interval for the 160 mg comparison is -1.22 to -0.48; the interval for the 80 mg comparison also lies entirely below zero. The registry record does not provide enough detail to independently verify the interval construction or its assumptions.

General statistical context: interval width depends on variability, sample size, and the method used. A narrow interval indicates greater precision in the estimated difference than a wide interval, while an interval that includes zero would leave more uncertainty about the direction of the difference under that interval method. An interval does not account automatically for multiplicity, bias, incomplete outcome capture, or limitations in the trial population.

What are the planning figures?

The sample-size illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects set at a stated fraction of the observed effect. The displayed estimates are participants per arm for each comparison, rather than total participants across all groups. The registry record’s original design assumptions and sample-size justification are not reported. These illustrations are planning exercises based on observed estimates; they are not observed power and do not show the probability that this completed trial detected an effect.

General statistical context: power is the probability, under a chosen assumed effect and analysis model, of rejecting the null hypothesis at the chosen significance level. Power is meaningful as a planning quantity only in relation to assumptions about the effect, variability, allocation, and analysis. Because smaller effects are harder to distinguish from random variation, planning for a smaller effect generally requires more participants, all else equal. The illustrations are not a substitute for the trial’s original design plan, which is not reported in the registry record.

Finally, multiplicity and missingness are distinct issues. Multiplicity concerns the number of outcomes and comparisons being interpreted; missingness concerns incomplete outcome information. The registry lists multiple outcomes and does not report a multiplicity adjustment. Its primary endpoint description specifies what was counted for dropouts, but does not state a general missing-data analysis strategy. Those omissions constrain how fully the posted inferential results can be audited.

11. Confidence Intervals and Precision

The primary estimates are accompanied by confidence intervals for each comparison with placebo. For the 80 mg group, the mean difference was -0.77 flares per participant, and the interval estimate lies wholly below zero. For the 160 mg group, the mean difference was -0.85, with a confidence interval from -1.22 to -0.48. Both posted intervals therefore point to a lower average flare count in the active group under the comparison method used.

In general, a confidence interval describes uncertainty around an estimate under the assumptions of the interval method. It is not a guarantee that the true effect lies within the interval, and it does not account automatically for sources of uncertainty that were not included in the analysis. For example, an interval does not by itself resolve concerns about multiple comparisons, missing outcomes, or the suitability of a statistical model.

The group standard deviations provide context for the variation in observed counts: 1.59 in placebo, 0.77 with 80 mg, and 0.54 with 160 mg. Those values are descriptive and should not be mistaken for standard errors or confidence limits. The reported sample sizes for the primary outcome were 79, 80, and 80 participants in the respective groups. The size of a confidence interval depends on both sample size and variability, as well as on the analysis method.

The unadjusted p-values are reported as p < 0.001 for both primary comparisons. Their small size does not make the effect estimate exact; the intervals remain the more direct description of precision. The registry record does not report details sufficient to establish whether the interval method incorporated any adjustments or modeling choices beyond the posted comparisons. Since the registry lists several outcomes and contrasts, the intervals should also be interpreted alongside the absence of a reported multiplicity strategy.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations for two-arm comparisons. The entries are participants per arm, not total participants across the trial; the outcome is not a time-to-event endpoint, so the figures are not total event counts. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects set at 100%, 75%, or 50% of the observed effect.

The 80% power column gives the planned number of participants per arm under those assumptions for an analysis designed to have an 80% probability of detecting the specified effect, if that effect and the assumptions were true. The 90% power column gives the corresponding participants per arm for a 90% probability. These are prospective planning quantities, not claims about what happened in the completed trial. This is not observed power.

For example, for the primary comparison of rilonacept 80 mg with placebo, planning for 100% of the observed effect gives 42 participants per arm for 80% power and 56 for 90% power. Planning for 75% of the observed effect gives 74 participants per arm for 80% power and 98 for 90% power. For the 160 mg comparison, the corresponding figures are 31 and 41 for 100% of the observed effect, and 55 and 73 for 75% of the observed effect.

The pattern reflects a general planning principle: a smaller effect is harder to distinguish from random variation, so it requires more participants per arm, all else equal. These estimates use the observed effect as a starting point and do not reproduce the trial’s original planning. The registry record does not report the original sample-size justification, target power, assumed effect, or any assumptions used when the trial was designed. The curve should be interpreted in the same way as the tabulated planning figures: as a visualization of assumed effects and corresponding sample-size requirements, not as an observed trial outcome.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.770; pooled standard deviation σ = 1.247.
2. n = 2 × (1.96 + 0.842)² × 1.247² / -0.770² = 41.2, rounded up to 42 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.77                      # observed difference in means
sigma <- 1.24673050122116                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(829829)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 42 (80% power), 56 (90% power)
 75% of observed effect: n per arm = 74 (80% power), 98 (90% power)
 50% of observed effect: n per arm = 165 (80% power), 221 (90% power)
power.t.test: 42.1 
Simulated power at n = 42 per arm: 0.803 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome, multiple secondary outcomes, and comparisons of each rilonacept dose with placebo. It does not report a multiplicity adjustment, a testing hierarchy, or which secondary results, if any, were intended to support confirmatory conclusions. When multiple hypotheses are tested, the chance of at least one apparently unusual result can increase. Adjustment procedures or a prespecified sequence of tests can address some of this issue, but the record does not describe such a procedure. The posted p-values are therefore read as unadjusted comparisons and should not be treated as if they account for all outcomes and contrasts.

The record also lists no reported analysis entries. This does not establish that no analyses were conducted; it means that analyses are not reported in the registry record. The precise tests, model specifications, assumptions, handling of protocol deviations, and planned approach to secondary outcomes are not reported in the registry record. The original sample-size justification and any interim analyses are also not reported in the registry record.

For the primary outcome population, the registry specifies a full analysis set comprising randomized participants who received any study medication, analyzed according to treatment allocated at randomization. This is a stated population definition, but the record does not explain how participants who were randomized and did not receive study medication were handled. It also does not provide a participant flow account sufficient to reconcile every outcome denominator across all measures.

The primary endpoint description gives a specific rule for dropouts: only flares occurring before Day 112 were counted, whether they occurred during treatment or not. That rule clarifies the time window counted for participants who left early. It does not recover flare information after dropout or explain whether other methods were used to address incomplete observation. A general missing-data strategy, assumptions about missingness, and sensitivity analyses are not reported in the registry record.

These limitations affect how strongly the posted inferential results can be interpreted. They do not change the observed group summaries, but they leave uncertainty about the full analysis process and the sensitivity of conclusions to testing choices or missing outcome information. The absence of this information should not be filled by assuming a particular protocol or statistical plan.

15. 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: accidental overdose (1.3%), musculoskeletal chest pain (1.3%), depression (1.3%), pneumonitis (1.3%), abdominal hernia obstructive (1.2%).

The registry reports serious adverse events affecting 3 participants in each group. The listed groups at risk were 79 for placebo, 80 for rilonacept 80 mg, and 81 for rilonacept 160 mg. These are participant counts, not counts of all serious-event episodes, and the summary does not provide event-specific detail by treatment group beyond the listed serious terms. The deaths field has no reported value, so deaths are not reported in the registry record.

The registry also lists other adverse events affecting 8 participants in placebo, 16 in the 80 mg group, and 17 in the 160 mg group, with the corresponding groups at risk as stated above. These are separate summary counts and should not be combined with the serious-event counts. The record lists serious-event terms including accidental overdose, musculoskeletal chest pain, depression, pneumonitis, abdominal hernia obstructive, and liver abscess, with percentages of 1.3% or 1.2% attached to the terms. The registry summary does not provide enough detail to assign those terms to particular groups or to assess causal relationships.

Adverse-event summaries describe events recorded during the study; they do not by themselves establish whether an event was caused by treatment. The group counts are descriptive, and the registry record does not provide a full safety analysis or detailed event narratives. They should be read separately from the primary flare outcome.

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

The primary results show lower mean flare counts in the two rilonacept groups than in placebo during the stated Day 1 to Day 112 period. The reported unadjusted differences and confidence intervals indicate that the group-average comparisons favor lower counts in both active groups. This is a description of the posted randomized-trial data under the registry’s stated endpoint and population definition. It is not a claim that every participant had fewer flares, or that individual outcomes can be predicted from the group means.

The findings apply to the participants, treatment schedules, outcome definition, and follow-up recorded for this trial. They do not establish what happened beyond Week 16, under different dosing schedules, or in populations not described in the record. The numerical ordering of the two active-group means is not a direct dose comparison; the registry presents each dose versus placebo and does not report a statistical comparison between the doses.

The posted secondary summaries show a direction consistent with the primary result for several flare-related measures, but those outcomes are related and their comparisons are unadjusted. They do not provide independent replication. Results for flare days and higher-pain flare days are not reported in the registry record. The missing analysis details and absence of a reported multiplicity strategy also limit how much weight can be placed on the collection of inferential results as a whole.

The study’s stated objective includes safety, but the registry’s adverse-event counts are limited summaries. Equal counts of serious adverse events across groups do not, on their own, establish equal safety, and differences in other adverse-event counts do not establish causation. Further details about event type, timing, severity, and attribution are not fully reported in the registry record.

In general, a randomized design can support comparisons between allocated groups when conduct, outcome ascertainment, and analysis are appropriately handled. The registry record identifies randomization and masking, but it does not report all information needed to assess those features in detail. The statistical evidence should therefore be interpreted as the posted summaries and unadjusted comparisons, with the stated precision and reporting limitations in view.

17. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint matters. The primary measure counts recurrent flares rather than reducing the outcome to a single yes-or-no event. That allows the mean to reflect repeated episodes, while the secondary threshold outcomes offer a complementary view of how many participants experienced one or more or two or more flares. Different summaries can illuminate different features of the same clinical experience, but their overlap also means they should not be treated as independent evidence.

It also shows the value of reading an estimate alongside its uncertainty. The mean differences preserve the outcome’s original units, and the confidence intervals indicate the range of values compatible with the comparison method. A p-value alone would not show the scale or precision of the difference. Similarly, means and standard deviations are useful summaries but do not reveal the full distribution of participant-level counts.

Multiplicity is especially relevant when a trial reports more than one endpoint and compares more than one treatment group with placebo. Unadjusted findings can appear stronger than the evidence warrants if the number of statistical opportunities is ignored. Here, the registry lists several outcomes and does not report a multiplicity strategy, making it important to distinguish the primary comparison from the secondary results.

Finally, registry reporting is part of the evidence. The record identifies the main endpoint, population, group summaries, comparisons, and some safety counts, but leaves the original design assumptions and important analysis details unreported. Statistical interpretation depends not only on numerical results, but also on whether the analysis population, missing-data approach, and testing plan are clear enough to evaluate. This record is a useful case for separating what the posted numbers say from what the available documentation cannot establish.

18. Limitations

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

The registry record does not report the original sample-size calculation or the assumptions used to plan enrollment. The displayed planning illustrations are based on observed effects and cannot be used to reconstruct the original design. Interim analyses, stopping rules, and any monitoring procedures are not reported in the registry record.

The primary endpoint is a count, but the registry reports group means and standard deviations without a detailed account of the count distribution or the model used for inferential comparisons. It does not describe checks for skewness, excess zeros, over-dispersion, or unequal observation time. These are possible considerations for count outcomes in general; the record does not establish whether any were present in this trial. The exact methods used to produce the posted p-values and intervals are not fully described.

There is also limited information about missing data. The endpoint description says that for dropouts only flares occurring before Day 112 were counted, but the registry does not report sensitivity analyses, assumptions about outcomes after dropout, or a general approach to incomplete diary data. The primary analysis population excludes randomized participants who did not receive study medication, but the record does not provide a full accounting of how such participants were handled.

Several secondary outcomes are registered, while results for the flare-day measures are not reported in the registry record. No multiplicity adjustment or testing hierarchy is reported. The adverse-event summary gives counts but does not provide detailed group-specific descriptions for the serious-event terms, and deaths are not reported in the registry record. These reporting gaps limit assessment of the completeness and robustness of the results; they do not, by themselves, establish that a particular bias or problem occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: PREventative Study Against URate-lowering Drug-induced Gout Exacerbations 1 — NCT00829829.
• Registry record last updated 2017-04-28; status last verified 2017-03.
• Results first posted 2017-04-28.
• 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.

22. Record Summary

The registry describes a completed Phase 3 randomized, parallel-group, placebo-controlled study of rilonacept during initiation of allopurinol therapy in participants with intercritical gout. The registered groups received placebo, rilonacept 80 mg, or rilonacept 160 mg. The primary endpoint was the number of gout flares per participant from Day 1 to Day 112 (Week 16), in a full analysis set of randomized participants who received study medication.

Posted primary means were 1.06 for placebo, 0.29 for rilonacept 80 mg, and 0.21 for rilonacept 160 mg. Each dose-versus-placebo comparison had an unadjusted p < 0.001. Several related secondary summaries show a consistent direction, while results for flare days and higher-pain flare days are not reported in the registry record. Serious adverse events affected 3 participants in each group; deaths are not reported in the registry record.

The registry does not report the original sample-size justification, detailed analysis plan, multiplicity strategy, or general missing-data approach. Interpret the posted comparisons as unadjusted results with those documentation limits in mind.