Black Widow Spider Antivenin for Patients With Systemic Latrodectism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Black Widow Spider Antivenin for Patients With Systemic Latrodectism (NCT00657540), a randomized phase 3 study. The primary outcome is Number of Participants With Treatment Failure.

2. Clinical Question

The registry describes a phase III, multicenter, randomized, double-blind controlled study conducted in emergency departments; the design fields also record quadruple masking. The primary endpoint was not simply a pain score at one moment. It combined failure to complete the treatment phase because of insufficient improvement at specified assessment times with the need for commercially available antivenin or prescription pain medication for latrodectism symptoms during the treatment phase.

The central statistical contrast is between the numbers of participants meeting this treatment-failure definition in the Analatro and saline groups. The primary analysis covered the period from the start of the first dose infusion to 48 hours post-treatment. Secondary aims included early and broader pain reductions, drug-related adverse events, and serious drug-related adverse events. The registry record does not report additional detail about how investigators planned to balance these secondary aims against the primary question.

3. Trial Design

This was a phase III, randomized, parallel-group trial with quadruple masking, conducted at multiple centers. The registry lists an enrollment of 60 and the status as completed. The study start is recorded as 2009-10, and primary completion as 2014-10. Instituto Bioclon S.A. de C.V. is listed as the sponsor.

Participants were assigned to Analatro or normal saline. The posted primary outcome counts were 15.0 among 29.0 participants in the Analatro group and 24.0 among 31.0 participants in the saline group. The endpoint description identifies the analysis population as all subjects who were randomized and received any study drug, called the modified intent-to-treat population. The registry record does not report whether every randomized participant received treatment or how many participants were excluded from this analysis population.

The trial took place in emergency departments and concerned patients presenting within 24 hours of symptom onset. Its primary efficacy outcome was treatment failure by 48 hours after the start of the first dose infusion. The definition allowed more than one route to failure: insufficient clinically significant pain improvement at specified early assessments that led to not completing the treatment phase, or use of specified additional treatments for latrodectism symptoms during the treatment phase.

Although the registry records the trial as randomized and quadruple-masked, details such as the randomization sequence, allocation concealment, identities of the masked parties, and procedures for maintaining masking are not reported in the registry record. The trial's original sample-size justification and statistical plan are also not reported in the registry record. The planning illustrations based on the observed effect are separate from those original design details.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population consists of all subjects that were randomized and received any study drug (modified intent to treat population).

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: The analysis population consists of all patients that were randomized and received any study drug (modified intent-to-treat population).

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Treatment Failure, measured over From start of Dose 1 infusion to 48 hours post treatment.

The primary endpoint counts participants who met the trial's treatment-failure definition. The registry defines treatment failure as not achieving pain control during the treatment phase, up to 48 hours after the start of the first dose infusion. A participant could qualify by not completing the treatment phase because of insufficient clinically significant improvement in pain intensity relative to baseline at 60, 90, 120, or 150 minutes after the start of the first dose. A participant could also qualify by requiring commercially available antivenin or prescription pain medication for latrodectism signs and symptoms during the treatment phase through 48 hours.

This endpoint is used to represent a clinically consequential lack of pain control over a defined treatment period, rather than relying on a single pain measurement. Combining specified inadequate-response and additional-treatment criteria can capture more than one way a participant may fail to achieve the intended treatment-phase outcome. At the same time, a composite endpoint depends on each component's definition and occurrence. A count of treatment failures does not, on its own, show which criterion was met by each participant; that breakdown is not reported in the registry record.

The posted count is 15.0 among 29.0 participants for Analatro and 24.0 among 31.0 for saline. These are participant counts, not average pain scores. The time window and treatment-failure rules define what the counts mean; the endpoint should not be interpreted as a direct measure of pain intensity at one particular assessment.

7. Results Posted in the Registry

• Normal Saline: 77.4% (24/31) versus 51.7% (15/29) on control; risk difference 25.7 percentage points (95% CI 2.3 to 49.1), risk ratio 1.50 (1.00–2.23); unadjusted two-proportion z-test p = 0.037.

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 Participants With at Least 13 mm Reduction in Pain Score at 30 Minutes Post-Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Normal Saline: 35.5% (11/31) versus 44.8% (13/29) on control; risk difference -9.3 percentage points (95% CI -34.1 to 15.4), risk ratio 0.79 (0.42–1.48); unadjusted two-proportion z-test p = 0.460.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Normal Saline and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With at Least 13 mm Reduction in Pain Score at Any Time Point

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Normal Saline: 58.1% (18/31) versus 65.5% (19/29) on control; risk difference -7.5 percentage points (95% CI -32.0 to 17.1), risk ratio 0.89 (0.59–1.32); unadjusted two-proportion z-test p = 0.553.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Normal Saline and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address early pain reduction, pain reduction at any post-infusion time point, drug-related adverse events, and drug-related serious adverse events. Taken together, they provide broader context for the primary treatment-failure endpoint, but they do not all measure the same construct or time window. The pain-reduction outcomes use a thresholded change in pain score, whereas the primary outcome combines specified inadequate response and use of additional treatment.

The posted secondary pain comparisons do not show a consistent pattern of a larger response in the Analatro group. The early pain-reduction comparison and the any-time-point comparison have recalculated confidence intervals that include zero, and their reported chi-squared p-values are 0.230 and 0.277. These outcomes therefore do not provide a clear, stand-alone statistical confirmation of the primary comparison. Their results also should not be read as direct tests of the same endpoint definition.

Secondary outcomes generally carry less weight when many outcomes are examined without a reported multiplicity adjustment or prespecified hierarchy. Multiple testing increases the chance that at least one comparison will appear notable by chance. The registry record does not report whether an adjustment, hierarchy, or other multiplicity strategy was used. The secondary results are best regarded as contextual evidence rather than independent confirmatory findings.

The adverse-event outcomes relate to safety reporting, not pain efficacy. They also have limited event counts, particularly for serious events, so the available comparisons cannot provide a highly precise estimate of uncommon outcomes. The record's serious adverse event counts and overall adverse-event counts should be interpreted separately from the primary treatment-failure result.

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

• Number of Participants With at Least 13 mm Reduction in Pain Score at 30 Minutes Post-Treatment
• Drug-related Adverse Events
• Number of Participants With at Least 13 mm Reduction in Pain Score at Any Time Point
• Drug-related Serious Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: the outcome is whether a participant met the definition of treatment failure. A binary outcome is naturally summarized by the number of participants with the event and the number assessed in each group. The posted counts are 15.0 of 29.0 in the Analatro group and 24.0 of 31.0 in the saline group. The corresponding posted proportions are 0.517 and 0.774.

What does a risk difference express?

A risk difference subtracts one group's event proportion from the other group's event proportion. The reported recalculation uses saline relative to Analatro, producing an estimate of 0.257. A positive value in that direction means the observed event proportion was higher in the saline group. Unlike a relative measure, a risk difference is expressed on the absolute proportion scale. It is useful for describing the size of the observed separation between groups, but its value remains subject to sampling uncertainty.

What does a confidence interval add?

A confidence interval gives a range of estimates compatible with the observed data under the method's assumptions. For the recalculated primary risk difference, the interval is 0.023 to 0.491. Its lower limit is above zero, while the width of the interval shows that the underlying difference is not pinned down to a narrow range. A confidence interval is not a guarantee that the true value lies within the particular range, nor does it describe the range of individual participant outcomes.

How should the p-values be read?

A p-value evaluates how compatible the observed data are with a null hypothesis of no group difference, under the specified statistical method. The sponsor-reported chi-squared analysis gives p = 0.018. The unadjusted recalculation gives p = 0.037. Neither value measures the probability that the null hypothesis is true, the size of the effect, or the chance that a result will replicate. A smaller p-value is not automatically evidence of a more important or more precise effect.

The registry reports the sponsor analysis as chi-squared, but does not provide additional details sufficient to reproduce all of its choices. The recalculation is an unadjusted comparison based on posted summary counts. It is useful as a transparent check on the event-count contrast, but does not replace an analysis that may account for details absent from the registry record. The discrepancy field is false, so the registry data do not flag a discrepancy between the posted summary and reported analysis.

Why do methods matter for binary outcomes?

Different methods can test the same general null hypothesis while using different approximations or handling sparse data differently. A chi-squared method uses an approximation to a reference distribution. General statistical practice treats the suitability of that approximation as dependent on the observed data and the method's conditions. With a modest trial size, the choice of method can matter, especially when counts are small. The registry does not report enough method detail to compare all possible alternatives or assess whether any adjustment was used.

Confidence intervals and p-values answer related but distinct questions. The p-value summarizes compatibility with a null model under the chosen test. The interval conveys both direction and a range of plausible effect estimates under its calculation. Reading them together is more informative than treating a thresholded p-value as a complete summary. The interval suggests a positive saline-minus-Analatro risk difference under the recalculation, while also allowing a wide range of magnitudes.

What is over-dispersion, and does it apply?

General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. It is especially relevant to some count and clustered-data models. The primary outcome in this record is a binary participant count, and no over-dispersion parameter or model is reported. The registry record does not describe a model that would allow a specific over-dispersion assessment, so this concept should not be used to reinterpret the reported result.

Randomization supports a comparison between assigned groups, while masking is intended to reduce the influence of knowledge of assignment on care or assessment. Those design labels do not remove uncertainty or guarantee that all analysis assumptions hold. Details about allocation procedures, masking implementation, missing-data handling, and covariate adjustment are not reported in the registry record.

Finally, analysis population definitions matter. The primary description specifies randomized participants who received any study drug, rather than all randomized participants regardless of treatment receipt. That distinction can affect how broadly the result represents the randomized comparison. The registry record does not report participant-level disposition details or the handling of missing primary endpoint observations.

11. Confidence Intervals and Precision

The recalculated primary risk difference is 0.257, with a confidence interval from 0.023 to 0.491. This interval excludes zero under the recalculation, indicating that the data are not centered on an equal observed event proportion in the two groups. Its breadth is also important: the result is compatible with different magnitudes of difference, from near the lower end of the interval to a much larger value.

Precision is limited by the number of participants contributing to the comparison: 29.0 in the Analatro group and 31.0 in the saline group. The confidence interval captures sampling uncertainty under the calculation method, but it does not cover uncertainty arising from unreported design or analysis details, endpoint classification, or applicability to other settings. The registry record does not report a confidence interval for the sponsor's chi-squared analysis.

A confidence interval should not be interpreted as a range containing a fixed proportion of individual participants' outcomes. It concerns uncertainty about the group contrast. Nor does a confidence interval that excludes zero establish that the estimate is exact or that the same magnitude would be seen in another study. The interval and the observed counts should be considered together: the direction of the primary comparison is clear in these data, while the size of the difference remains imprecisely estimated.

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 illustrations are planning calculations based on fractions of the observed effect, not the trial's own design justification. Because the outcomes are binary participant counts, the figures are participants per arm, not total events. The calculations assume 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. The original trial's design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for 80% power under those planning assumptions and the specified effect. In plain terms, it represents a planning scenario in which the study would have an 80% chance of detecting that effect at the stated significance level, if the assumptions and effect were correct. The 90% power column gives the corresponding planning number for 90% power. These are not guarantees of detection in a future trial.

For the primary endpoint, planning for 100% of the observed effect gives 54 participants per arm for 80% power and 71 participants per arm for 90% power. Planning for 75% of the observed effect gives 100 and 133 participants per arm, respectively; planning for 50% gives 231 and 308 participants per arm. The sample requirements rise as the target effect becomes smaller, because a smaller group difference is harder to distinguish from random variation.

These figures are planning illustrations, not observed power. They do not indicate the probability that the completed trial's finding is true or the probability that the trial succeeded. They also should not be confused with the actual enrollment of 60 participants, which was the registry's total enrollment figure.

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 = 0.517; treatment proportion p₁ = 0.774; average p̄ = 0.646.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6764 = 1.3257.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6516 = 0.5484.
4. n = (1.3257 + 0.5484)² / (0.2570)² = 53.2, rounded up to 54 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 <- 0.517241379310345                          # control proportion
p1 <- 0.774193548387097                          # 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(657540)
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 = 54 (80% power), 71 (90% power)
 75% of observed effect: n per arm = 100 (80% power), 133 (90% power)
 50% of observed effect: n per arm = 231 (80% power), 308 (90% power)
power.prop.test: 53.2 
Simulated power at n = 54 per arm: 0.812 (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 the sponsor's primary analysis as a chi-squared comparison, with p = 0.018. Separately, the unadjusted recalculation from the posted group counts gives a risk difference of 0.257, a confidence interval from 0.023 to 0.491, and p = 0.037. Both analyses point to a difference in treatment failure between the groups, with the posted proportions higher in the saline group.

The recalculation makes the contrast and its uncertainty interpretable on the risk-difference scale. The sponsor-reported result is the analysis explicitly recorded by the trial registry. The registry does not provide sufficient detail to establish whether differences between the p-values arise from test implementation, adjustments, or another analytic choice. The discrepancy field is false, and no conflict between the posted outcome counts and the reported analysis is flagged.

The two p-values should therefore be retained with their methods attached: one is the sponsor-reported chi-squared result, and the other is an unadjusted recalculation from summary counts. The recalculation is not a substitute for participant-level analysis or a fully documented sponsor analysis. Details that would allow a complete reconstruction, including handling of missing outcomes and any other analytic adjustments, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary efficacy endpoint and multiple secondary outcomes. The primary endpoint is treatment failure by 48 hours. Secondary outcomes include early pain reduction, pain reduction at any time point, and drug-related adverse-event measures. Because several outcomes and comparisons are reported, multiplicity is relevant: the more statistical tests considered, the greater the chance that at least one result may appear notable even if no underlying group difference exists.

The registry record does not report a multiplicity adjustment, a formal testing hierarchy, or whether secondary outcomes were designated as confirmatory or exploratory. It also does not report an interim-analysis plan, stopping rules, or the original statistical analysis plan. Without those details, the secondary p-values should not be treated as if they had been adjusted or protected by a prespecified sequence of tests. This limitation does not change the recorded numbers, but it affects how strongly multiple results can be interpreted together.

The primary endpoint description specifies a modified intent-to-treat population consisting of randomized participants who received any study drug. This is an important population definition, but the registry record does not report how many randomized participants did not receive study drug, whether any participants were omitted from the primary analysis, or a participant disposition by reason.

Missing outcome data can affect a binary comparison if missingness is related to treatment group or outcome status. The registry record does not report the number of missing primary outcomes, the approach used to handle missing observations, or any sensitivity analyses for missing data. It is therefore not possible from the registry record to assess the influence of missingness on the primary estimate. These missing analysis details limit independent reconstruction and should be kept distinct from the observed treatment-failure counts.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cellulitis (3.2%), inadequate pain control (3.2%).

The serious adverse event listing records 0 serious events among 29 participants at risk in the Analatro group and 2 among 31 participants at risk in the normal saline group. The record lists cellulitis and inadequate pain control at 3.2% each among the top serious-event terms. It also records 0 deaths in each group. These are descriptive safety figures; the event counts alone do not establish whether an event was caused by study treatment.

The overall drug-related adverse-event counts are 26 among 29 participants at risk for Analatro and 27 among 31 for saline. The serious-event counts are much smaller than these overall counts, so the two measures should not be conflated. With only a small number of serious events recorded, estimates of differences in uncommon harms are inherently uncertain. The registry record does not provide a confidence interval for these safety comparisons or detailed event narratives.

The brief summary describes an aim to assess whether serious drug-related adverse events in Analatro-treated patients occurred at a rate greater than one in 10 (10%). The posted group counts are descriptive and do not, by themselves, provide a complete statistical assessment of that aim. The registry record does not report the specific analysis used for that threshold question.

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

The primary result describes the proportion of participants meeting a defined treatment-failure endpoint during the treatment phase through 48 hours. In the posted results, the count was 15.0 among 29.0 participants assigned to Analatro and 24.0 among 31.0 assigned to saline. The sponsor-reported chi-squared analysis gives p = 0.018, while the unadjusted recalculation estimates a risk difference of 0.257 with a confidence interval from 0.023 to 0.491.

These data show a group difference in the recorded primary endpoint in this trial. They do not give a precise estimate of every possible treatment effect: the recalculated interval is broad, the endpoint combines more than one failure criterion, and component-specific counts are not reported. The primary result also should not be treated as a direct measurement of pain severity at a single time point.

The result does not, by itself, establish how the same comparison would perform in other settings, among populations with different characteristics, or over time periods not included in the endpoint. The registry record describes an emergency-department population presenting within 24 hours of symptom onset and a treatment-failure window through 48 hours. It does not report a broader basis for extending the findings beyond that study context.

The secondary results, multiplicity information, missing-data details, and safety counts provide important context but do not erase the distinctions between outcomes. In particular, a lack of a clear secondary comparison is not automatically a contradiction of the primary endpoint, because the outcomes differ in definition and timing. Conversely, the primary result does not establish conclusions about every secondary efficacy or safety measure.

Statistical evidence should be separated from medical advice. These registry results describe what was recorded and the uncertainty around a group comparison; they do not determine an individual patient's care. Clinical interpretation requires context beyond the statistical summaries, including information not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definitions matter in clinical research. Treatment failure was not a single pain-score threshold at one assessment; it included inadequate improvement leading to failure to complete the treatment phase and use of additional specified treatment. That definition yields an outcome with practical relevance to the treatment period, while making it essential to understand the composite criteria before interpreting the total count.

It also shows why an effect estimate and its uncertainty should be read alongside a p-value. The posted primary counts favor a lower treatment-failure proportion in the Analatro group, and the recalculated risk difference has a confidence interval excluding zero. At the same time, the interval is wide, emphasizing that statistical evidence of a difference does not mean the size of the difference is known precisely.

The comparison also demonstrates the value of distinguishing a sponsor-reported analysis from a simple recalculation of posted summary counts. Both are useful, but they answer through stated methods that are not fully interchangeable. Transparent reporting of analysis details, missing data, and multiplicity plans allows readers to assess how conclusions depend on statistical choices.

Finally, the relatively limited number of participants and serious events highlights a general issue in clinical trials: an endpoint can show a group pattern while rare outcomes remain difficult to estimate precisely. Planning illustrations based on an observed effect can help convey how required sample sizes grow when smaller effects are targeted, but they are not the original trial rationale or a measure of observed power.

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.

The registry record describes enrollment of 60, with primary analysis counts of 29.0 and 31.0 in the two groups. This is a limited evidence base for estimating a treatment-failure difference and especially for assessing uncommon serious adverse events. The recalculated primary confidence interval is broad, so the size of the group difference remains uncertain.

The primary endpoint is a composite of more than one criterion. The record does not provide counts for each component, so it is not possible to determine how much of the total contrast came from insufficient early improvement versus use of additional treatment. The endpoint is also limited to the treatment phase through 48 hours; the registry record does not establish outcomes beyond that window.

The analysis population is defined as randomized participants who received any study drug. Participant disposition and the handling of missing primary outcomes are not reported in the registry record. The registry also does not report the original sample-size justification, detailed statistical analysis plan, multiplicity strategy, interim analyses, or enough detail to reconstruct every aspect of the sponsor's analysis.

The secondary outcomes use different definitions and time points, and the registry does not report a multiplicity adjustment or testing hierarchy. Safety figures include few serious events, limiting precision for uncommon harms. Finally, the emergency-department presentation context and onset window define the population described; the registry record does not establish how directly the findings apply beyond that context.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Black Widow Spider Antivenin for Patients With Systemic Latrodectism — NCT00657540.
• Registry record last updated 2018-04-03; status last verified 2018-03.
• Results first posted 2017-09-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes NCT00657540, a completed phase III, multicenter, randomized, parallel-group trial with quadruple masking, sponsored by Instituto Bioclon S.A. de C.V. The study compared Analatro with normal saline in patients with systemic latrodectism. Enrollment was 60; the recorded study start was 2009-10 and primary completion was 2014-10.

The primary endpoint counted participants with treatment failure through 48 hours after the start of the first dose infusion. The posted counts were 15.0 among 29.0 Analatro participants and 24.0 among 31.0 saline participants. The sponsor-reported chi-squared result was p = 0.018. An unadjusted recalculation gave a risk difference of 0.257, with a confidence interval from 0.023 to 0.491.

Secondary outcomes addressed pain reduction and adverse events. Missing-data handling, the original sample-size justification, and a multiplicity strategy are not reported in the registry record.