Investigation of Sacroiliac Fusion Treatment (INSITE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigation of Sacroiliac Fusion Treatment (INSITE) (NCT01681004), a randomized na study. The primary outcome is Subject Success.

2. Clinical Question

The clinical question combines a comparison of treatment strategies with a composite outcome. It does not ask only whether pain improved: success also depended on device-related serious adverse events, neurologic worsening, and surgical re-intervention. The registry describes the primary analysis as intent to treat, assigning success or failure to subjects randomized and treated, with early withdrawals deemed failures. It also describes the analysis population as modified intent to treat. The precise distinction between those descriptions is not explained in the registry record.

The study was randomized and parallel, but masking was listed as none. The posted results therefore describe outcomes in the trial groups without blinding listed in the registry. The question is about the outcomes recorded for these participants and this composite definition; it does not by itself establish how the strategies compare for every patient or for outcomes not captured by the trial.

3. Trial Design

INSITE, or Investigation of Sacroiliac Fusion Treatment, was a randomized, parallel-group study sponsored by SI-BONE, Inc. The registry lists an enrollment of 159 and a phase of NA. The listed conditions were degenerative sacroiliitis and sacroiliac joint disruption. Study start was recorded as 2012-09, primary completion as 2015-02, and status as completed.

The two groups were the iFuse Implant System and non-surgical management. The surgical group received placement of iFuse implants in the affected SI joint. The non-surgical management description lists medications, SI joint injection, physical therapy, and RF ablation of the SI joint. Allocation was randomized; masking was listed as none. The registry does not report further details about sequence generation, allocation concealment, or whether outcome assessors were masked.

The primary outcome was subject success at 6 months. The analysis is described as intent to treat, with outcomes assigned to all subjects randomized and treated and early withdrawals treated as failures. The population field separately says that a modified intent-to-treat approach was used. More detail about the population definition is not reported in the registry record.

The registry lists 25 outcome measures and 24 posted secondary outcomes. These include SI joint pain VAS improvement at several follow-up times and improvement in back dysfunction. The posted primary and secondary comparisons are binary counts of participants meeting the relevant outcome. The registry does not report the trial's original sample-size justification, planned interim analyses, or a detailed statistical analysis plan. No reported analyses are listed for the posted secondary outcome records, so the posted group counts and recalculated comparisons should be read as registry results rather than as a description of a fully reported analysis plan.

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: Of the 442 patients who were screened for participation at 19 sites, 159 (37.8%) were enrolled. Eleven subjects withdrew before treatment (1 before randomization and 10 after randomization but before any treatment was performed), yielding a total of 148 subjects who were enrolled, randomized and treated.

Primary Endpoint: 6 Months

Reasons for not completing this period:

Study Completion

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: A modified intent-to-treat approach was used.

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: Of the 442 patients who were screened for participation at 19 sites, 159 (37.8%) were enrolled. Eleven subjects withdrew before treatment (1 before randomization and 10 after randomization but before any treatment was performed), yielding a total of 148 subjects who were enrolled, randomized and treated (102 to iFuse Implant System \& 46 to NSM).

6. Primary Endpoint

The registry lists the primary outcome as Subject Success, measured over 6 months.

The primary endpoint, subject success at 6 months, is a composite. A participant had to meet all of its listed components: reduction from baseline in VAS back pain score by at least 20 mm, no device-related serious adverse events, no neurologic worsening, and no surgical re-intervention. The measure is a count of participants classified as successful, rather than a continuous average pain score.

A composite can summarize several clinically relevant dimensions in one outcome and can count a participant as unsuccessful if any required component is not met. That makes the endpoint broader than pain improvement alone, but it also means the overall result does not show which component most often determined success. Component-specific primary results are not reported in the registry record.

The registry describes the primary endpoint analysis as intent to treat: outcomes were assigned to subjects randomized and treated, and those who withdrew early were deemed failures. It also identifies the analysis population as modified intent to treat, without explaining the exact population rule. The success counts therefore need to be interpreted in light of the registry's stated handling of early withdrawal and this incompletely described population definition.

This endpoint is useful for comparing the observed proportion meeting a prespecified combined threshold across the randomized groups. It does not capture every possible benefit or harm, and a binary success classification does not convey the degree of improvement among those counted as successes or the reason for failure among those who were not.

7. Results Posted in the Registry

• Non-Surgical Management: 26.1% (12/46) versus 82.4% (84/102) on control; risk difference -56.3 percentage points (95% CI -71.0 to -41.6), risk ratio 0.32 (0.19–0.52); unadjusted two-proportion 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.

Improvement in SI Joint Pain VAS Score at 1 Month

• 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:
  • Non-Surgical Management: 28.9% (13/45) versus 84.0% (84/100) on control; risk difference -55.1 percentage points (95% CI -70.2 to -40.0), risk ratio 0.34 (0.22–0.55); 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 Non-Surgical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Improvement in Si Joint Pain VAS Score at 3 Months

• 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:
  • Non-Surgical Management: 39.5% (17/43) versus 87.0% (87/100) on control; risk difference -47.5 percentage points (95% CI -63.5 to -31.4), risk ratio 0.45 (0.31–0.66); 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 Non-Surgical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Improvement in SI Joint Pain VAS Score at 6 Months

• 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:
  • Non-Surgical Management: 27.9% (12/43) versus 83.2% (84/101) on control; risk difference -55.3 percentage points (95% CI -70.5 to -40.0), risk ratio 0.34 (0.21–0.55); 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 Non-Surgical Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary pain-improvement outcomes at 1 month, 3 months, and 6 months show a consistent broad pattern: more participants in the iFuse group met the improvement outcome than in the non-surgical management group at each listed follow-up. This aligns directionally with the primary composite result, particularly because pain improvement is one component of that composite. It does not make the secondary outcomes interchangeable with primary success, which also required the absence of specified safety and subsequent-treatment events.

These outcomes can add context about pain improvement over follow-up, but they do not independently reproduce the full primary endpoint. The secondary list also includes back dysfunction outcomes, but the posted values summarized in the registry record do not include a full set of reported analyses for all listed measures. A complete account of their definitions and analytical handling is not reported in the registry record.

Secondary results generally carry less confirmatory weight when there are many outcomes or follow-up times and no reported strategy for controlling multiplicity. With repeated statistical comparisons, the chance of at least one apparently notable result can increase. This is a general statistical concern, not evidence that any specific result in this trial is false. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints.

The registry's secondary analyses field is empty for the posted outcome records. The recalculated comparisons can describe the group pattern in the available counts, but should not be mistaken for a prespecified, fully documented analysis. The consistent direction across the listed pain outcomes is useful descriptive context; it does not resolve concerns about missing-data handling, open-label assessment, or the interpretation of multiple outcomes.

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

• Improvement in SI Joint Pain VAS Score at 1 Month
• Improvement in Si Joint Pain VAS Score at 3 Months
• Improvement in SI Joint Pain VAS Score at 6 Months
• Improvement in SI Joint Pain VAS Score at 12 Months
• Improvement in SI Joint Pain VAS Score at 24 Months
• Improvement in Back Dysfunction
• Improvement in Back Dysfunction
• Improvement in Back Dysfunction

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is reported? The primary and posted secondary outcomes are binary counts: each participant is classified as meeting or not meeting an outcome definition. The registry reports the number meeting the definition and the number in the group used for that outcome. A proportion expresses the count meeting the outcome relative to the relevant group denominator. Because the endpoint is binary, the analysis compares proportions rather than comparing average scores.

What does the risk difference mean? A risk difference subtracts one group's event proportion from the other's. Here, the comparison is expressed as non-surgical management relative to the iFuse group. A negative value therefore indicates a lower observed proportion meeting the outcome in the non-surgical group. The estimate is an absolute contrast in proportions, not a relative ratio. The risk difference is especially interpretable when the question concerns the difference in the share of participants meeting a defined outcome.

What does the confidence interval add? A confidence interval gives a range of values compatible with the observed data under the statistical method used. Its endpoints reflect sampling uncertainty; they do not account automatically for all sources of uncertainty, such as bias, outcome misclassification, unreported analysis choices, or missing data. If a confidence interval for a risk difference includes zero, the data are compatible with no difference under that interval method. The primary interval reported in this trial is entirely negative for the stated comparison direction.

How should the p-value be read? The p-value is reported as unadjusted. In general, it measures how incompatible the data are with a specified null model of no group difference, assuming the model and its conditions are appropriate. A small p-value is not a measure of the size or clinical importance of an effect. It does not show that the result is free of bias and is not the probability that the null hypothesis is true. Since the registry does not describe a multiplicity plan, the unadjusted p-values should not be treated as if they account for all outcomes and time points examined.

Why does randomization matter? Random allocation is intended to make treatment groups comparable on average with respect to factors present before assignment. It supports an interpretation of group differences as comparisons of assigned strategies, subject to how participants were analyzed and whether follow-up and outcome measurement were handled appropriately. Randomization does not guarantee that the groups are identical, and it cannot prevent bias arising after assignment. The registry lists randomized allocation but does not report details of sequence generation or allocation concealment.

What is the relevance of masking? Masking can reduce the influence of knowledge of treatment assignment on outcome assessment, reporting, or care. The registry lists masking as none. This is relevant for an endpoint that includes a pain measure, which depends on participant report, as well as event and re-intervention criteria. The record does not report whether any outcome assessment procedures were otherwise standardized or independently adjudicated, so those details should not be assumed.

How should the analysis population be understood? The primary endpoint description says intent to treat and states that outcomes were assigned to all subjects randomized and treated; early withdrawals were deemed failures. The population description says modified intent to treat. The registry does not explain exactly how these formulations were reconciled or which participants were excluded, if any. Early withdrawals classified as failures are one explicit rule, but the record does not provide a complete account of missing observations or other analysis-population decisions.

What does a recalculated comparison represent? A recalculated comparison uses posted group summary counts to obtain a simple, unadjusted contrast and its interval or test. It is not necessarily the same as a sponsor's prespecified model or a covariate-adjusted analysis. The registry record does not list reported analyses for the secondary endpoints. Accordingly, the recalculated secondary comparisons should be understood as descriptive comparisons based on the posted counts, rather than as a substitute for a more detailed analysis report.

Why is over-dispersion not central? Over-dispersion concerns variation greater than expected under certain count or rate models. The posted outcomes are binary participant counts, not repeated event rates or a continuous measure modeled with a dispersion parameter. The registry lists no dispersion estimate for these outcomes. In general, model choice should match the outcome and design; the registry does not provide enough detail to identify any additional modeling choices beyond the posted binary comparisons.

What can the statistical results establish? They quantify the observed group contrast and its sampling uncertainty for the defined outcomes. They do not, on their own, explain mechanisms, identify which composite component drove the difference, or guarantee that the estimate applies to other populations. Interpretation must also consider the open-label listing, the analysis-population description, and the absence of a reported multiplicity plan and detailed statistical analysis plan.

11. Confidence Intervals and Precision

The primary risk difference is -0.563, with a 95% confidence interval from -0.710 to -0.416. The interval is entirely below zero for the comparison of non-surgical management relative to iFuse. This indicates that, under the interval method, the data are not compatible with a zero risk difference at the corresponding confidence level. It also shows that the estimated size of the difference is not known exactly: a range of negative contrasts remains compatible with the posted data.

The interval describes sampling precision, not the full uncertainty around the result. It does not account for possible bias from the absence of masking, uncertainty about the exact modified intent-to-treat population, unreported outcome-assessment details, or the handling of missing data beyond the stated early-withdrawal rule. Nor does it isolate the contribution of each element in the composite endpoint.

The confidence interval should be read together with the group counts and the outcome definition. The proportions concern success under a composite rule, not a continuous change in pain or a single adverse event. The interval is relatively far from zero, but its endpoints still allow a range of effect magnitudes. The registry does not report a separate precision analysis for the individual composite components.

For secondary outcomes, intervals are also posted for the recalculated comparisons, but those endpoints are related and were assessed across multiple time points. Their individual intervals do not by themselves address uncertainty from multiplicity. The registry does not report an adjustment strategy for repeated secondary comparisons. Thus, the primary interval gives a measure of precision for its stated contrast, while broader conclusions across several outcomes require additional caution.

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 based on the observed effect, not the trial's original design justification. The original trial's sample-size assumptions are not reported in the registry record. For these binary outcomes, the planning figures are participants per arm, not total participants or total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect.

The 80% power column gives the estimated participants per arm under which a future study would have an 80% chance of detecting the specified effect at the stated significance level, if the planning assumptions and effect were correct. The 90% power column gives the corresponding planning size for a higher chance of detection. These are design calculations, not guarantees that a future study will obtain a significant result.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. The figures are sensitive to the observed effect used as their starting point; an effect estimated in one trial can be an uncertain basis for planning a future study.

This is not observed power. It is a set of prospective illustrations calculated from the observed effect and stated assumptions. The registry does not report that these values were used in designing INSITE. For any time-to-event outcomes, the stated convention would be total events, but the primary and secondary outcomes are participant counts, so the displayed planning quantities refer to participants per arm.

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 = 0.824; treatment proportion p₁ = 0.261; average p̄ = 0.542.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7046 = 1.3810.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5815 = 0.4894.
4. n = (1.3810 + 0.4894)² / (-0.5627)² = 11.0, rounded up to 12 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 <- 0.823529411764706                          # control proportion
p1 <- 0.260869565217391                          # 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(1681004)
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 = 12 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 26 (90% power)
 50% of observed effect: n per arm = 42 (80% power), 56 (90% power)
power.prop.test: 11 
Simulated power at n = 12 per arm: 0.867 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists 25 outcome measures and 24 posted secondary outcomes, including pain improvement at different follow-up times and repeated back dysfunction outcomes. When multiple outcomes are examined, the chance of observing at least one result that appears statistically notable can rise. Statistical plans can address this through a prespecified hierarchy or an adjustment for multiple comparisons. A multiplicity strategy is not reported in the registry record.

The primary endpoint is identified, but details of any ordering or confirmatory role for secondary endpoints are not reported. The unadjusted p-values associated with the recalculated comparisons should therefore be interpreted as individual comparisons rather than as evidence that the overall family of secondary questions has been controlled for multiplicity. This does not negate the observed patterns; it limits how strongly they can support separate confirmatory claims.

Missing-data handling is only partly described. The primary endpoint description says that early withdrawals were deemed failures and that outcomes were assigned to subjects randomized and treated. The population field says modified intent to treat, but the registry record does not define that population in detail or explain how the two descriptions fit together. It does not provide a complete account of missing observations at each follow-up, reasons for missingness, or sensitivity analyses under alternative assumptions.

The primary and secondary outcome denominators vary across posted follow-up results. The registry does not explain all reasons for those denominator differences. They should not be interpreted as a complete accounting of participant flow or missingness. No imputation method or other missing-data model is reported in the registry record.

Analysis populations and missing-data assumptions can affect binary success counts, particularly when withdrawal is assigned failure for a composite endpoint. Without a fuller report, the reader cannot assess whether alternative reasonable assumptions would materially change the results. The registry also does not report interim analyses, a detailed statistical analysis plan, or a stated procedure for handling all secondary comparisons.

15. 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: contralateral sij pain (9.8%), degenerative disease - spine (6.9%), meniscal tear (3.9%), back pain (2.9%), ankle fracture (2.2%).

The registry reports serious adverse events among 38 of 102 participants at risk in the iFuse Implant System group and 12 of 46 at risk in the non-surgical management group. For other adverse events, the reported counts are 69 of 102 and 35 of 46, respectively. These are posted group counts; they do not by themselves establish that an event was caused by the assigned treatment.

The listed serious adverse event terms include contralateral SIJ pain at 9.8%, degenerative disease - spine at 6.9%, meniscal tear at 3.9%, back pain at 2.9%, ankle fracture at 2.2%, and ipsilateral - SIJ pain at 2.2%. The registry also reports 1 death in each group. The record does not provide enough detail in these summary fields to characterize timing, severity beyond the serious classification, relatedness, or participant-level overlap among events.

Safety counts should be read alongside the primary endpoint, which included absence of device-related serious adverse events as one component. The adverse-event summaries are not a complete causal comparison and do not substitute for detailed event narratives or exposure-adjusted analyses, which are not reported in the registry record.

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

The posted results show a clear difference in the observed proportion meeting the primary composite success definition at 6 months: 84 of 102 in the iFuse group and 12 of 46 in the non-surgical management group. The reported risk difference, confidence interval, and unadjusted p-value indicate that the observed contrast is statistically distinguishable from zero under the comparison method used. That is a statement about these trial data and this outcome definition.

The result does not mean that every participant receiving iFuse experienced improvement, or that no participant in non-surgical management did. It also does not establish that the difference was due solely to pain improvement. Success required multiple conditions, and the registry does not report component-level primary results that would show which requirements most affected the group counts.

The study was randomized, which supports a comparison of assigned groups, but masking was listed as none. The registry does not detail the outcome-assessment process, full participant flow, or the exact modified intent-to-treat population. Those features matter when interpreting a pain-related outcome and a composite that includes adverse events and re-intervention.

The result should not be generalized automatically to people who differ from the trial population, to different procedures or non-surgical care, or to outcomes and follow-up not reported in the record. The listed comparison is not a personalized prediction and does not establish the balance of all potential benefits and harms. The registry record does not report a complete analysis of every endpoint, nor a multiplicity strategy for secondary outcomes.

In statistical terms, the estimate captures an observed group contrast, while the confidence interval describes its sampling precision under the method used. Neither measure removes uncertainty from study conduct, measurement, missing data, or choice of outcome. The most defensible interpretation is therefore bounded: the posted counts favor the iFuse group on the defined composite in this randomized comparison, while the record leaves important analytical and component-level questions unanswered.

17. Why This Trial Matters Statistically

INSITE illustrates why a clinical trial result cannot be reduced to a p-value. Its primary endpoint is a binary composite combining improvement in back pain with the absence of specified serious adverse events, neurologic worsening, and surgical re-intervention. That construction determines what the success counts mean and prevents treating them as a pain score alone.

The comparison also illustrates the value of absolute measures. A risk difference expresses the observed contrast in the proportions meeting the endpoint, while the confidence interval shows the range of estimates compatible with the data under the method used. The combination communicates both direction and uncertainty more clearly than a significance label alone.

At the same time, the registry record demonstrates the importance of transparent methods. It lists randomized allocation, no masking, an intent-to-treat description, and a modified intent-to-treat population, but does not fully reconcile the population descriptions or report all missing-data and analysis details. Those omissions limit assessment of how robust the posted results are to analytical choices.

The secondary pain outcomes provide related context, but multiple follow-up comparisons need a prespecified interpretation strategy. Without a reported multiplicity plan, secondary findings should be treated as supportive descriptive evidence rather than as a collection of independent confirmations. Likewise, planning calculations based on the observed effect are illustrations, not evidence of the trial's original design rationale or of power achieved after completion.

Overall, the trial is statistically instructive because it pairs a substantial observed group contrast with issues that require careful reading: composite outcome construction, open-label assessment, analysis-population definitions, multiplicity, and registry reporting detail. These considerations apply broadly when interpreting randomized clinical trial results.

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.

Several limitations specific to this registry record constrain interpretation. Masking is listed as none. Since the primary endpoint includes VAS pain improvement, outcome reporting and assessment may be sensitive to awareness of assigned treatment. The registry does not describe independent adjudication, assessor masking, or other safeguards for subjective components.

The registry's description of the primary analysis uses both intent-to-treat language and a modified intent-to-treat population label. It states that subjects randomized and treated were assigned success or failure and that early withdrawals were deemed failures, but does not define the modified population fully. The denominators reported across outcomes also vary, and the reasons are not described in detail. This limits assessment of participant inclusion and missing-data sensitivity.

The primary measure is composite, but the record does not give component-specific primary counts. It is therefore not possible from the posted summary to determine how much each criterion contributed to success or failure. The registry lists serious and other adverse-event counts and selected serious-event terms, but does not provide a detailed account of timing, treatment relatedness, overlap, or exposure-adjusted event rates in the summary fields.

The registry does not report the original sample-size justification, a detailed statistical analysis plan, interim analyses, or a multiplicity strategy. Secondary analyses are not listed as reported analyses. Recalculated comparisons based on posted counts cannot fill those reporting gaps or establish that an analysis was prespecified. The available registry results consequently support a description of the recorded comparisons but not a full audit of trial conduct and analysis.

Finally, enrollment and registry outcome summaries do not alone establish how representative the participants were or how the results apply outside this trial. Further eligibility, site, participant-flow, and follow-up details are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Investigation of Sacroiliac Fusion Treatment (INSITE) — NCT01681004.
• Registry record last updated 2017-08-25; status last verified 2017-08.
• Results first posted 2017-08-25.
• 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

INSITE (NCT01681004) was a completed randomized, parallel-group study sponsored by SI-BONE, Inc. It compared surgical placement of the iFuse Implant System with non-surgical management for degenerative sacroiliitis or sacroiliac joint disruption. The registry lists enrollment of 159, no masking, study start in 2012-09, and primary completion in 2015-02.

The primary outcome was subject success at 6 months, a composite that required back-pain improvement and absence of specified adverse or subsequent-treatment events. Success was reported for 84 of 102 in the iFuse group and 12 of 46 in the non-surgical management group. The reported risk difference was -0.563, with a 95% confidence interval from -0.710 to -0.416 and an unadjusted p-value of <0.001.

The registry also posts secondary pain-improvement outcomes, adverse-event counts, and planning illustrations based on observed effects. Important details—including the original sample-size justification, a detailed analysis plan, multiplicity handling, and a full account of missing data—are not reported in the registry record.