Efficacy and Safety Study of Adalimumab in Treatment of Hidradenitis Suppurativa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of Adalimumab in Treatment of Hidradenitis Suppurativa (NCT01468207), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Hidradenitis Suppurativa Clinical Response (HiSCR) at Week 12.

2. Clinical Question

The study was a Phase 3, randomized, double-masked, parallel-group trial. The primary endpoint assessed a specified change in inflammatory lesions and draining fistulas over the initial treatment period. This makes the central question one of comparative response by Week 12, rather than a comparison of longer-term treatment sequences. The registry record also reports outcomes in baseline Hurley Stage subgroups, which describe disease stage at enrollment. Those subgroup results offer additional context, but they do not replace the overall randomized comparison as the main trial question.

3. Trial Design

The registry record describes a completed Phase 3, randomized, double-masked, parallel-group study of adalimumab and placebo for moderate to severe HS. Enrollment was 307. The primary endpoint was assessed from Baseline (Week 0) up to Week 12, during Period 1. In that period, the placebo group received placebo, while the active-treatment group received adalimumab every week using the loading and maintenance schedule described in the record.

The Week 12 results compare the groups as randomized at baseline. The primary analysis population was the intention-to-treat population, defined as all participants randomized at Baseline (Week 0). The endpoint was also presented by baseline Hurley Stage. The record describes Stage II and Stage III classifications and notes how participants with disease across anatomic regions were classified. No primary Stage I result appears among the posted endpoint groups.

After Period 1, the registry describes a Period 2 lasting up to 24 weeks, with treatment sequences that included placebo followed by weekly adalimumab, weekly adalimumab followed by placebo, and different adalimumab schedules. Participants who began on placebo received adalimumab in Period 2; participants who began on adalimumab were re-randomized to one of the listed sequences. These later sequences are distinct from the initial placebo-controlled Week 12 comparison. The record does not report enough detail to reconstruct how each later-period analysis handled treatment switching or follow-up.

Although the record identifies randomization, masking, and a parallel model, details such as the randomization procedure, allocation concealment, and the operational masking procedures are not reported in the registry record. The trial's original sample-size justification and original statistical analysis plan are also not reported in the registry record. Therefore, the posted results can be described, but the planned design assumptions behind the trial's enrollment cannot be verified from this record.

4. Participant Flow and Accounting

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

Treatment Period 1

Reasons for not completing this period:

Treatment Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intention-to-treat (ITT) population, defined as all participants who were randomized at Baseline (Week 0), was analyzed overall and by baseline Hurley Stage

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Hidradenitis Suppurativa Clinical Response (HiSCR) at Week 12, measured over Baseline (Week 0) up to Week 12.

The primary endpoint is the percentage of participants achieving Hidradenitis Suppurativa Clinical Response (HiSCR) at Week 12. A participant met the definition with at least a 50% reduction from baseline in abscess and inflammatory nodule (AN) count, alongside no increase in abscess count and no increase in draining fistula count. Missing endpoint data were handled with non-responder imputation: participants with missing data were counted as non-responders.

This composite response definition combines a reduction in inflammatory lesion burden with safeguards against worsening in abscesses or draining fistulas. In general, a prespecified responder endpoint can make the clinical target easier to interpret than a change in a score alone: it states what degree and pattern of change qualifies as a response. The percentage summarizes how commonly that criterion was met in each group. It does not show the full range of individual changes, and two participants classified the same way could have different starting levels or different changes in particular lesion types.

The endpoint was assessed in the randomized population and additionally reported by baseline Hurley Stage. The registry's definition specifies the assessment window as Baseline (Week 0) up to Week 12. The endpoint therefore addresses response over the initial treatment period, not durability after Week 12. The registry record does not report a separate endpoint definition for longer-term maintenance of HiSCR in the later treatment sequences.

7. Results Posted in the Registry

• Adalimumab Every Week (EW): 41.8% (64/153) versus 26.0% (40/154) on control; risk difference 15.9 percentage points (95% CI 5.4 to 26.3), risk ratio 1.61 (1.16–2.23); unadjusted two-proportion z-test p = 0.003.
• Placebo - Baseline Hurley Stage II: 29.8% (25/84) versus 26.0% (40/154) on control; risk difference 3.8 percentage points (95% CI -8.2 to 15.8), risk ratio 1.15 (0.75–1.75); unadjusted two-proportion z-test p = 0.531.
• Placebo - Baseline Hurley Stage III: 21.4% (15/70) versus 26.0% (40/154) on control; risk difference -4.5 percentage points (95% CI -16.4 to 7.3), risk ratio 0.83 (0.49–1.39); unadjusted two-proportion z-test p = 0.464.
• Adalimumab Every Week (EW) - Baseline Hurley Stage II: 44.6% (37/83) versus 26.0% (40/154) on control; risk difference 18.6 percentage points (95% CI 5.9 to 31.3), risk ratio 1.72 (1.20–2.46); unadjusted two-proportion z-test p = 0.004.

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.

Percentage of Participants With Baseline Hurley Stage II Who Achieved Abscess and Inflammatory Nodule (AN) Count of 0, 1, or 2 at Week 12

• 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:
  • Adalimumab Every Week (EW) - Baseline Hurley Stage II: 28.9% (24/83) versus 28.6% (24/84) on control; risk difference 0.3 percentage points (95% CI -13.4 to 14.1), risk ratio 1.01 (0.63–1.63); unadjusted two-proportion z-test p = 0.961.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adalimumab Every Week (EW) - Baseline Hurley Stage II and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving At Least 30% Reduction and At Least 1 Unit Reduction From Baseline in Patient's Global Assessment of Skin Pain (NRS30) - At Worst at Week 12 Among Participants With Baseline Skin Pain NRS ≥ 3

• 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:
  • Adalimumab Every Week (EW) - Baseline NRS at Worst ≥ 3: 27.9% (34/122) versus 24.8% (27/109) on control; risk difference 3.1 percentage points (95% CI -8.3 to 14.5), risk ratio 1.13 (0.73–1.74); unadjusted two-proportion z-test p = 0.594.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adalimumab Every Week (EW) - Baseline NRS at Worst ≥ 3 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Week 12 in Modified Sartorius Score

• 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:
  • Adalimumab Every Week (EW): mean -24.40 versus -15.70 on control; difference -8.70 (95% CI -19.75 to 2.35), standardized effect d = -0.18; z-test p = 0.123.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Adalimumab Every Week (EW) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoints cover lesion counts, patient-reported skin pain, and change in modified Sartorius score. Across these outcomes, the results do not form a uniform pattern of clear group separation. The sponsor analyses and the recalculations differ in method and precision, so the secondary evidence should be considered outcome by outcome rather than collapsed into a single overall conclusion.

These endpoints complement the primary HiSCR result by looking at specific clinical features and a score-based change. They are related to HS burden, but they are not interchangeable with the primary responder definition. A participant could meet one endpoint's criterion without meeting another's, because the outcome definitions, populations, and measurement scales differ. The secondary results therefore add context rather than serving as direct confirmation or refutation of the primary endpoint.

The registry reports several outcomes and subgroup analyses, but does not report whether the statistical plan adjusted for multiple testing or identified a hierarchy among secondary endpoints. In general, when many outcomes are tested, the chance of at least one nominally unusual result increases unless the analysis accounts for multiplicity. Unadjusted secondary p-values should consequently carry less inferential weight than a prespecified primary analysis. They can be useful for describing patterns and generating questions, but they do not independently establish a definitive treatment effect across all outcome domains.

The record does not report a multiplicity-adjusted interpretation or a complete protocol-level hierarchy. It is therefore not possible to determine from the posted results whether the secondary analyses were confirmatory, exploratory, or governed by another prespecified strategy. The safest reading is to treat them as supporting descriptive evidence, with attention to their intervals, sample sizes, analysis populations, and the methods used, rather than to select isolated p-values as decisive findings.

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

• Percentage of Participants With Baseline Hurley Stage II Who Achieved Abscess and Inflammatory Nodule (AN) Count of 0, 1, or 2 at Week 12
• Percentage of Participants Achieving At Least 30% Reduction and At Least 1 Unit Reduction From Baseline in Patient's Global Assessment of Skin Pain (NRS30) - At Worst at Week 12 Among Participants With Baseline Skin Pain NRS ≥ 3
• Change From Baseline to Week 12 in Modified Sartorius Score

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Cochran-Mantel-Haenszel analysis for the overall primary comparison. It also reports Chi-squared analyses for the Hurley Stage subgroup comparisons. The recalculated contrasts are simple, unadjusted comparisons based on the posted group summaries. For the continuous secondary endpoint, the sponsor reports an ANCOVA analysis. These methods answer related but not identical statistical questions, so the reported sponsor analyses and recalculations should be read as separate results.

What does a Cochran-Mantel-Haenszel analysis do?

In general, a Cochran-Mantel-Haenszel method combines information across strata to estimate an association or contrast while accounting for stratification. An adjusted result can differ from a crude, unadjusted comparison because it uses the stratified structure of the analysis. The registry labels the primary result as an adjusted mean difference and reports the method as Cochran-Mantel-Haenszel. The record does not name all adjustment variables or provide enough detail to reproduce the model specification. The adjustment should therefore be described as the sponsor reports it, without assuming which additional covariates or strata were used.

How should the Chi-squared subgroup analyses be read?

In general, a Chi-squared test assesses whether categorical outcomes differ across groups under the test's assumptions. Here, the sponsor reports Chi-squared analyses for the Stage II and Stage III comparisons. The subgroup contrasts are distinct analyses, not a single test of whether treatment effects differ between stages. A formal test of interaction, which would address whether the treatment contrast varies by stage, is not reported in the registry record. Separate subgroup p-values alone do not establish that effects differ between subgroups.

What is different about the recalculated estimates?

The recalculated binary comparisons use the posted outcome proportions and arm counts to produce unadjusted contrasts and confidence intervals. They do not reproduce the sponsor's adjustment. General statistical practice treats such recalculations as checks on the posted summary data, not as replacements for a prespecified trial analysis. Because the record flags a discrepancy, the sponsor's own analysis takes precedence for the trial's reported inference. The recalculation can still help readers understand the simple comparison, provided its unadjusted status is kept clear.

For a binary response, an unadjusted risk difference expresses the difference in response probabilities between groups. Its confidence interval describes the range of values reasonably compatible with the data and the calculation's assumptions. If that interval includes zero, the data are compatible with no difference under that unadjusted calculation; if it excludes zero, it is less compatible with a zero difference at the corresponding confidence level. This interpretation does not account for multiplicity or adjustments not included in the recalculation.

How should the continuous secondary outcome be understood?

The modified Sartorius score outcome is reported as a least-squares mean change, with standard error, and the sponsor reports an ANCOVA comparison. In general, ANCOVA compares groups while adjusting for selected covariates, often including baseline outcome values. The registry identifies the method and reports a least-squares mean difference, but the full covariate specification is not reported in the registry record. The recalculated contrast is approximate and unadjusted, using posted summaries; it does not recreate the sponsor's ANCOVA model.

In general, a standard error describes the estimated sampling variability of an estimate, while a confidence interval communicates uncertainty on the scale of the effect. The secondary score's reported changes are group-level estimates and do not show the distribution of individual participant changes. The registry record does not provide enough distributional detail to assess score behavior, outliers, or whether model assumptions were checked.

Why does over-dispersion matter?

Over-dispersion is a general concern when observed variability in data exceeds what a statistical model assumes. It can make standard errors too small if the model does not account for the extra variability, which in turn can make confidence intervals too narrow and p-values too small. The primary endpoint is binary, and the record identifies categorical methods rather than a count model. Over-dispersion is therefore not a reported feature of the primary analysis. More generally, the registry record does not report diagnostic checks or enough model detail to evaluate all assumptions.

The p-values indicate how incompatible the observed results are with a specified null hypothesis under the analysis assumptions; they are not probabilities that the null hypothesis is true, nor measures of clinical importance. The registry's reported p-values and the recalculated unadjusted p-values may differ because the underlying analyses differ. The record does not report whether p-values were adjusted for multiple endpoints, subgroup analyses, or repeated testing. Those omissions limit the strength of conclusions across the full set of outcomes.

11. Confidence Intervals and Precision

The sponsor's primary analysis reports a 95% confidence interval from 5.3 to 26.5 for the adjusted mean difference, with an estimate of 15.9. This interval conveys uncertainty around the sponsor's adjusted contrast. It is compatible with a range of positive differences under that analysis, rather than identifying one exact effect as known. The p-value of 0.003 is a related measure of statistical compatibility with a null difference, but it does not describe the size or practical importance of the result.

The recalculated unadjusted interval for the overall primary comparison is 0.054 to 0.263 on the risk-difference scale. That recalculation is not the same quantity or analysis as the sponsor's adjusted mean difference, and the registry flags a discrepancy. The sponsor's own analysis takes precedence. Comparing interval endpoints across those representations without accounting for their scales and methods would be misleading.

Confidence intervals for the subgroup comparisons are broader in relation to their estimates than the overall reported interval, reflecting less precision in those subgroup estimates. Some recalculated subgroup intervals include zero, while the posted sponsor analyses report separate subgroup p-values. These are not inconsistent in the sense that the estimates and inference methods are not identical. The record does not report a formal interaction test, and subgroup intervals should not be used alone to claim that treatment contrasts differ by stage.

In general, a confidence interval is a method for expressing the uncertainty that would arise from repeated sampling under a statistical model. It does not mean that there is a specified probability that the true effect lies in the particular interval after the data have been observed. Precision also depends on the estimate's scale and method. The registry does not provide all details needed to independently reproduce the sponsor's adjusted interval, so its reported interval should be read as the sponsor's analysis.

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 estimates are planning illustrations based on the observed effect, not the trial's own design calculations. For these outcomes, figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The registry record's original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future two-arm study to have an 80% probability of detecting the specified effect under the planning assumptions, if that effect is the true one and the assumptions hold. The 90% power column gives the corresponding planning number for a 90% probability. These are design targets, not guarantees of a result and not retrospective measures of what the completed study achieved.

Rows labeled as planning for 100%, 75%, or 50% of the observed effect illustrate how the required enrollment changes when the target effect changes. A smaller target effect generally requires more participants to distinguish it from no effect with the same planned power and significance level. When the observed effect is very small, the resulting planning figures can become very large; this reflects the assumptions used for the illustration, not a recommendation or a feasibility judgment.

These values are not observed power. Observed power is not a useful substitute for reading the estimate and its confidence interval after a trial. The planning illustrations instead show how sensitive hypothetical future enrollment requirements are to the assumed effect size. Their interpretation also depends on the stated equal-allocation and normal-approximation assumptions, and they do not reproduce the trial's original design process.

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 = 0.260; treatment proportion p₁ = 0.418; average p̄ = 0.339.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6695 = 1.3121.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6600 = 0.5555.
4. n = (1.3121 + 0.5555)² / (0.1586)² = 138.7, rounded up to 139 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 <- 0.25974025974026                          # control proportion
p1 <- 0.418300653594771                          # 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(1468207)
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 = 139 (80% power), 186 (90% power)
 75% of observed effect: n per arm = 241 (80% power), 321 (90% power)
 50% of observed effect: n per arm = 523 (80% power), 700 (90% power)
power.prop.test: 138.7 
Simulated power at n = 139 per arm: 0.803 (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 reports the primary comparison using a Cochran-Mantel-Haenszel analysis, with an adjusted mean difference of 15.9, a 95% confidence interval from 5.3 to 26.5, and p = 0.003. The sponsor also reports Chi-squared analyses for the Hurley Stage subgroups and an ANCOVA analysis for change in modified Sartorius score. These are the trial's own reported analyses in the registry record.

The simple recalculation uses posted group summaries and is unadjusted. Its role is to offer a check on the broad numerical pattern, not to reproduce the sponsor's analysis. The registry flags a discrepancy between the sponsor result and the recalculation. In keeping with that discrepancy, the sponsor's own analysis takes precedence. The adjusted sponsor estimate and the unadjusted recalculation should not be combined or described as if they were the same statistic.

The registry does not provide enough detail to independently recreate every sponsor model, including the full adjustment specifications. Consequently, the sponsor-reported estimates, intervals, and p-values should be quoted as reported, while any recalculated result should be clearly identified as an unadjusted check. Neither analysis alone resolves questions about multiplicity, missing-data sensitivity, or generalizability; those require additional information not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when many statistical tests are conducted. In general, testing multiple outcomes, subgroups, or time points without an adjustment can increase the chance of at least one result appearing statistically unusual by chance. This trial record includes a primary endpoint, several secondary endpoints, and baseline Hurley Stage subgroup analyses. Whether and how the original analysis plan controlled multiplicity is not reported in the registry record. The posted p-values should therefore be read as reported test results, not assumed to be multiplicity-adjusted.

The primary endpoint used non-responder imputation: participants with missing data were considered non-responders. This gives a defined rule for the primary binary analysis. However, the record does not state the amount of missing primary outcome data, the reasons for missingness, or whether the missingness differed between groups. It also does not report sensitivity analyses under alternative missing-data assumptions. Without those details, the robustness of the result to missing outcomes cannot be fully assessed.

The primary population is described as the intention-to-treat population, comprising all participants randomized at Baseline (Week 0). That definition supports interpretation according to initial assignment for the primary comparison. The record's descriptions of later treatment sequences include re-randomization after Period 1, but do not provide enough detail to characterize the analysis population for every later-period outcome. The primary result should not be conflated with analyses of those later sequences.

Subgroup findings require additional caution. The record provides results by baseline Hurley Stage, but does not report a formal treatment-by-stage interaction test or whether those subgroup analyses were prespecified. Separate tests within subgroups do not establish that the treatment effect differs by subgroup. Details of the original statistical analysis plan, including interim analyses, multiplicity control, and subgroup planning, are not reported in the registry record.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hidradenitis (4.2%), ectopic pregnancy (2.1%), abortion induced (2.1%), abdominal pain (0.7%), pneumonia (0.7%).

The registry reports serious adverse event counts by treatment period and sequence. During Period 1, the placebo group had 5 serious adverse events among 152 at risk, and the weekly adalimumab group had 3 among 153 at risk. Period 2 counts are separately listed for placebo followed by weekly adalimumab and for the three sequences beginning with weekly adalimumab. These later-period groups had different treatment histories and at-risk counts, so the figures should be read as period- and sequence-specific descriptions rather than as a single direct comparison.

The registry lists serious adverse event terms including HIDRADENITIS at 4.2%, ECTOPIC PREGNANCY at 2.1%, ABORTION INDUCED at 2.1%, ABDOMINAL PAIN at 0.7%, PNEUMONIA at 0.7%, and HEPATITIS A ANTIBODY POSITIVE at 0.7%. The record does not provide a full event-level narrative in these summary details, and it does not report deaths. Serious adverse events are not the same as all adverse events; the record also gives counts for other adverse events, but these summaries do not describe severity, duration, or causal attribution.

These figures are descriptive safety data, not evidence that an event was caused by a treatment. The registry record does not report enough information to make a complete comparative safety assessment across the changing treatment sequences.

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

The primary result describes a difference between randomized groups in the proportion meeting the registry's HiSCR definition at Week 12. The sponsor's analysis reports an adjusted difference with a confidence interval that excludes zero and a p-value of 0.003. This is evidence of a group contrast under that analysis and its assumptions. It is not a statement that every participant responded, nor does it capture the full range of individual outcomes.

HiSCR is a defined composite response, not a complete measure of every aspect of HS. It combines lesion-count requirements and a no-increase condition for abscesses and draining fistulas. The percentage meeting that definition does not by itself report symptom burden in every domain, quality of life, long-term disease course, or whether an individual participant experienced a meaningful change. Those outcomes should not be inferred from this endpoint.

The comparison covers the initial period through Week 12. The record also describes later treatment sequences, but the primary result does not establish the durability of response after the initial period or the relative effects of every sequence. The treatment changes in Period 2 make those results a different question from the initial randomized comparison.

Statistical significance does not by itself determine clinical importance. The effect estimate and its interval describe the scale and uncertainty of the group contrast, while judgments about importance require a clinically justified threshold and broader context. Such a threshold is not reported in the registry record. The results also do not show how treatment should be selected for any particular person, and they should not be used as individual medical advice.

Finally, a randomized trial can support a comparison within its enrolled study population and procedures, but its results may not apply identically to people or care settings not represented. The registry record does not provide enough detail about participant characteristics beyond the stated adult moderate to severe HS population to assess transportability fully.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary outcome is a prespecified binary responder definition in a randomized, double-masked comparison. The response rule is explicit: a specified reduction in abscess and inflammatory nodule count, without an increase in abscess or draining fistula count. That clarity lets readers interpret what the reported percentages represent, while also making clear that the endpoint compresses a range of participant experiences into response versus non-response.

The posted result also illustrates why the analysis method matters. The sponsor reports an adjusted primary analysis, while a simple recalculation from posted summaries is unadjusted and the record flags a discrepancy. Reporting both perspectives requires keeping their estimands and methods distinct. The sponsor analysis takes precedence for the trial's own inference, but a transparent distinction between adjusted and unadjusted results helps readers understand why two numerical summaries need not match exactly.

The subgroup and secondary results highlight another recurring challenge in clinical research: multiple comparisons can create a scattered pattern of p-values and estimates. Without a reported multiplicity strategy or formal interaction assessment, isolated subgroup or secondary findings deserve more cautious interpretation than the primary comparison. Their role is to describe additional dimensions of the data, not automatically to establish separate confirmatory claims.

Finally, the sample-size illustrations show how planning depends strongly on the effect targeted. They are explicitly based on observed effects and stated hypothetical assumptions, rather than the trial's original design. This distinction is important when using completed-trial results to plan future work: observed estimates are uncertain, and planning around a smaller effect can require substantially more participants. The registry record does not report the original design justification, so the illustrations cannot be used to infer why the trial enrolled its recorded number.

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 important design and analysis details unreported. It does not include the original sample-size justification, the full statistical analysis plan, the randomization procedure, allocation concealment details, or the operational masking procedures. It also does not identify the complete adjustment specification for the sponsor's primary analysis. These omissions limit independent assessment and reproduction of the sponsor's analysis.

The record flags a discrepancy between the sponsor analysis and the recalculated unadjusted comparison. The sponsor result takes precedence, but the difference reinforces that the recalculation is not a substitute for the trial's own analysis. The posted summaries do not permit a full audit of how the sponsor obtained its adjusted estimates.

For the primary endpoint, missing outcomes were classified as non-responses. The amount and pattern of missingness and sensitivity analyses are not reported in the registry record. Multiplicity control for the secondary outcomes and subgroup analyses is also not reported. In addition, the record does not report a formal interaction test for treatment effects across Hurley Stage groups, so separate subgroup results cannot establish effect modification.

The secondary outcome summaries offer limited detail about distributions and model assumptions. For the continuous score, the registry reports least-squares means, standard errors, and an ANCOVA result, but not the complete covariate specification or diagnostic checks. For safety, the summaries provide counts by period and sequence but not a full account of event timing, duration, severity, or attribution. Deaths are not reported in the registry record.

These limitations concern what can be assessed from the registry record; they do not establish that particular methods or procedures were absent from the full trial documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of Adalimumab in Treatment of Hidradenitis Suppurativa — NCT01468207.
• Registry record last updated 2021-07-07; status last verified 2021-07.
• Results first posted 2015-10-28.
• 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.

23. Record Summary

The registry describes NCT01468207 as a completed Phase 3, randomized, double-masked, parallel-group study of adalimumab in adults with moderate to severe hidradenitis suppurativa. Enrollment was 307. The primary endpoint was the percentage achieving HiSCR at Week 12, comparing weekly adalimumab with placebo during Period 1.

The sponsor reports an adjusted primary difference of 15.9, with a 95% confidence interval from 5.3 to 26.5 and p = 0.003. The registry also reports results by baseline Hurley Stage, secondary endpoints, later treatment sequences, and adverse event summaries. The record flags a discrepancy with the simple unadjusted recalculation; the sponsor's own analysis takes precedence.

Important details, including the original sample-size justification, multiplicity strategy, and missing-data sensitivity analyses, are not reported in the registry record. The primary result is specific to the stated Week 12 response definition and does not establish longer-term outcomes.