Impact of Applying a Bandage Skin Hydrogel on the Pains of the Head and Neck in Patients With Cancer of Head and Neck Treated With Radiotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Impact of Applying a Bandage Skin Hydrogel on the Pains of the Head and Neck in Patients With Cancer of Head and Neck Treated With Radiotherapy (NCT01520701), a randomized phase 3 study. The primary outcome is Impact of Applying a Bandage Hydrogel Skin on Head and Neck Pains.

2. Clinical Question

3. Trial Design

The registry classifies NCT01520701 as a phase 3 randomized trial with a parallel-group design and no masking. The listed enrollment is 130. The sponsor is Centre Francois Baclesse, the recorded start is 2012-02, the primary completion is 2022-10, and the status is completed. These registry entries describe the recorded design and timeline, but do not establish how the trial was conducted at each site or whether all enrolled participants contributed to every outcome.

The two groups were Ialuset® Application and Bandage Skin Hydrosorb. The arm descriptions state that the assigned product was applied to the cervical skin during radiotherapy. The intervention list names bandage skin Hydrotac® and Ialuset®; elsewhere, the bandage is called Hydrosorb®. The record therefore uses different names for the hydrogel bandage across its entries. The posted primary outcome counts are 6 of 37 in the Ialuset® group and 10 of 40 in the bandage group. These outcome denominators are not a substitute for the enrollment figure and should not be treated as a complete account of participant flow.

Random allocation is intended, in general, to balance measured and unmeasured prognostic factors across groups on average. In this trial, the record identifies the allocation as randomized but does not report the sequence-generation method, allocation concealment, or masking. With no masking recorded, participants and clinical staff may have known the assigned application; whether outcome assessors were masked is not reported in the registry record. The record lists chemotherapy dose reduction as a secondary outcome, but does not provide a fuller description of the protocol, analysis population, or original design assumptions.

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

Analysis population for the primary outcome, as defined in the registry: 5 patients do not answer to the score algia EVA rating scale at the inclusion visit.

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: 15 patients did not meet eligibility criteria, 33 patients do not have answer to questionnaries after the end of the treatment by radiotherapy

6. Primary Endpoint

The registry lists the primary outcome as Impact of Applying a Bandage Hydrogel Skin on Head and Neck Pains, measured over end of radiotherapy (2 months after inclusion).

The primary endpoint counts participants whose pain score worsened by three or more points on the EVA rating scale between baseline, identified as D0, and the end of treatment. The planned assessment time is the end of radiotherapy, stated as 2 months after inclusion. The endpoint is binary: each participant is classified according to whether the specified deterioration occurred, and the group result is the number of participants meeting that criterion.

A change threshold can make a continuous rating scale easier to interpret as a clinically defined event, but it also discards information about the size and direction of changes that do not meet the threshold. A participant just below the cutoff and one with no worsening are grouped together for this endpoint, while participants meeting the cutoff are counted as events. The outcome therefore addresses the frequency of a specified degree of deterioration, not average pain scores or all changes in pain.

The record says 5 patients did not answer the pain rating scale at the inclusion visit. It does not explain how this baseline missingness was handled in the primary analysis, whether all randomized participants had endpoint assessments, or whether other pain measurements were collected. Those details matter because the endpoint relies on comparing baseline and end-of-treatment scores. The posted counts describe the outcome summaries available in the registry, not a complete account of the measurement process.

7. Results Posted in the Registry

• Bandage Skin Hydrosorb: 25.0% (10/40) versus 16.2% (6/37) on control; risk difference 8.8 percentage points (95% CI -9.1 to 26.7), risk ratio 1.54 (0.62–3.82); unadjusted two-proportion z-test p = 0.343.

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.

Chemotherapy Dose Reduction

• 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:
  • Bandage Skin Hydrosorb: 18.2% (8/44) versus 21.1% (8/38) on control; risk difference -2.9 percentage points (95% CI -20.1 to 14.4), risk ratio 0.86 (0.36–2.08); unadjusted two-proportion z-test p = 0.744.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bandage Skin Hydrosorb and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome, chemotherapy dose reduction during 36 months after radiotherapy. The overall pattern is one of uncertainty rather than a clear separation between groups: the posted event counts are equal, and the estimated contrast has a confidence interval that includes zero and allows differences in either direction. That pattern does not establish that the groups are equivalent, nor does it independently confirm the primary pain finding.

The secondary endpoint addresses a different event over a longer timeframe than the primary endpoint, which is pain deterioration measured at the end of radiotherapy. Agreement or disagreement between these outcomes would not necessarily be expected because they capture distinct aspects of treatment experience and occur over different periods. The primary result is itself imprecise, so the secondary outcome cannot resolve uncertainty about the pain comparison.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis. They may be more vulnerable to chance findings when several outcomes or comparisons are examined, and their interpretation depends on whether they were planned, how missing data were handled, and whether any multiplicity strategy was specified. The registry record does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or reported analyses beyond the posted summary. Accordingly, the secondary result is best treated as descriptive and hypothesis-generating rather than as a definitive confirmatory finding.

The record labels chemotherapy dose reduction as a secondary outcome, but does not give the rationale for its inclusion, detailed definition, or handling of changes over time. The posted figures therefore provide a limited view of this outcome. They can be read alongside the primary result as part of the registry’s overall evidence, while keeping the different endpoint, timeframe, and uncertainty in view.

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

• Chemotherapy Dose Reduction

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level measure: whether pain deteriorated by at least the stated threshold from baseline to the end of radiotherapy. For a binary outcome, each group’s event count is interpreted relative to the participants contributing outcome data in that group. The posted counts are 6 of 37 for Ialuset® Application and 10 of 40 for Bandage Skin Hydrosorb. The contrast is expressed as a risk difference, defined generally as the event risk in one group minus the event risk in the comparison group. A risk difference of zero represents equal observed risks; a positive value means a higher observed risk in the first-named group under the subtraction order used.

The posted primary risk-difference estimate is 0.088. Its confidence interval ranges from -0.091 to 0.267. Because the interval spans zero, the data are compatible with no difference as well as with differences favoring either group in the sense of a higher or lower event risk. The interval describes uncertainty in the estimated contrast under the method used; it is not a range containing a fixed proportion of individual participant outcomes. The confidence level and precise interval procedure are not reported in the registry record.

The unadjusted p-value for the primary comparison is 0.343. In general, a p-value evaluates how unusual data at least as discordant with a specified null model would be if that model and the test assumptions held. It does not measure the size or clinical importance of an effect, and it does not tell the probability that the null hypothesis is true. The record identifies this result as unadjusted. It does not report the test procedure used for the sponsor’s original analysis or any covariate-adjusted model.

Risk ratios and odds ratios can also express a binary-outcome contrast, but their interpretation differs from a risk difference. A risk ratio compares the event risks multiplicatively; an odds ratio compares the odds. Such relative measures can appear numerically more dramatic or less intuitive depending on how common the event is. The registry’s posted primary comparison includes relative measures, but the risk difference is used for the main explanation because it directly describes an absolute contrast in event risk. No conversion or recalculation is needed to understand the direction and uncertainty reported in the record.

The secondary outcome is also binary: whether chemotherapy dose reduction was recorded during 36 months after radiotherapy. The posted counts are 8 in each group, with outcome denominators of 38 for Ialuset® Application and 44 for Bandage Skin Hydrosorb. Its unadjusted risk-difference estimate is -0.029, with a confidence interval from -0.201 to 0.144 and an unadjusted p-value of 0.744. As with the primary outcome, the interval includes zero and allows a range of possible group contrasts. The registry record does not provide reported analyses for this outcome beyond the posted summary comparison.

General statistical interpretation also depends on outcome completeness and the analysis population. The primary endpoint requires a baseline and follow-up pain score. The record notes 5 patients without an answer at the inclusion visit, but does not state the missing-data strategy, the number with missing end-of-treatment scores, or whether the primary comparison followed an intention-to-treat principle. The outcome denominators differ from one another and from the listed enrollment, but the record does not explain participant flow or the reasons for these differences. This limits assessment of whether missingness could have affected the estimates.

Dispersion is not applicable in the same way to a simple event count as it is to a continuous measurement, and no dispersion statistic is posted for these outcomes. For count outcomes, the central statistical issues are the event definition, the denominator, and uncertainty in the event risk and its contrast. If counts were modeled using a distribution that assumes variance equal to the mean, over-dispersion—variation greater than that assumption allows—could make standard errors too small and intervals too narrow. That is a general concern for some count models; the registry record does not report such a model for these binary endpoints.

The registry identifies the study as randomized and parallel-group, but the sequence-generation and concealment procedures are not reported in the registry record. Nor are the original statistical analysis plan, the primary test, adjustments for baseline variables, or any interim analyses. The posted analysis count is zero, and no reported analyses are listed. These omissions mean the summaries can be interpreted descriptively, but the record does not permit a full audit of the prespecified analysis or deviations from it.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.088, with a confidence interval from -0.091 to 0.267. This interval is broad and crosses zero. In practical statistical terms, the observed counts do not pin down the size or even the direction of the underlying contrast precisely. The data are compatible with a lower event risk in the bandage group, little difference, or a higher event risk, within the interval’s limits.

A confidence interval conveys uncertainty in an estimate under the statistical method used. In general, it is not a guarantee that the true value lies inside the particular interval, nor does it describe the range of outcomes for individual participants. The confidence level and interval construction method are not reported in the registry record, so the interval should be interpreted as posted rather than as a fully documented inferential procedure.

The secondary risk-difference estimate is -0.029, with a confidence interval from -0.201 to 0.144. It too spans zero and permits differences in both directions. Neither interval establishes that the groups are equivalent. Demonstrating equivalence or non-inferiority generally requires a prespecified margin and an analysis designed for that question; such details are not reported in the registry record.

Precision depends on the amount of outcome information and on the frequency of events, among other factors. The posted primary comparison includes 6 and 10 events, while the secondary comparison includes 8 events in each group. These counts and the reported intervals indicate that the registry results leave substantial uncertainty around the group contrasts. The p-values do not replace that assessment: interval width and the range of plausible effects are essential to understanding how precisely the trial estimates each difference.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrative requirements for participants per arm, not total participants and not total events. They are based on the observed effect and do not describe the original trial’s sample-size calculation. The record states the planning assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The original design assumptions and any sample-size justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the planning model were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities for a future study under an assumed effect; they are not probabilities that the observed trial result is correct.

The planning rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The estimates increase as the effect used for planning becomes smaller: a subtler difference is harder to distinguish from random variation, so more participants are needed to reach the same target power under otherwise unchanged assumptions. For the primary outcome, the listed participant requirements per arm range from 332 to 1,222 for 80% power and from 444 to 1,635 for 90% power across those effect assumptions. These are planning illustrations, not observed power.

Such calculations are sensitive to the observed effect, which can be unstable in a small study, and to assumptions about allocation, testing, and the outcome model. The record does not report whether the trial’s own design used these assumptions. The figures should therefore be read as hypothetical planning guidance based on the posted result, not as evidence that the completed trial had a particular probability of finding a difference.

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 = 0.162; treatment proportion p₁ = 0.250; average p̄ = 0.206.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5720 = 1.1212.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5687 = 0.4786.
4. n = (1.1212 + 0.4786)² / (0.0878)² = 331.7, rounded up to 332 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 <- 0.162162162162162                          # control proportion
p1 <- 0.25                          # 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(1520701)
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 = 332 (80% power), 444 (90% power)
 75% of observed effect: n per arm = 567 (80% power), 759 (90% power)
 50% of observed effect: n per arm = 1,222 (80% power), 1,635 (90% power)
power.prop.test: 331.7 
Simulated power at n = 332 per arm: 0.802 (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 record lists one primary outcome and one secondary outcome, but does not report how the analysis plan addressed multiple comparisons. When several outcomes are tested, the chance of at least one apparently unusual result can increase if each is judged independently. General methods to address this include a prespecified hierarchy, adjustment of significance thresholds, or emphasis on estimation rather than repeated significance testing. Whether any such approach was used in this trial is not reported in the registry record.

The primary endpoint description notes that 5 patients did not answer the EVA pain rating scale at the inclusion visit. Because the endpoint is defined as deterioration from baseline to the end of treatment, missing baseline ratings may affect whether a participant can be classified. The registry does not state whether these patients were excluded, whether values were imputed, or how the issue was otherwise handled. It also does not report the number of missing end-of-treatment scores or a detailed participant flow for the primary endpoint.

The posted primary outcome denominators are 37 and 40, while the secondary denominators are 38 and 44. The registry lists enrollment as 130, but does not explain the relationship between enrollment and the outcome-specific denominators. It is therefore not possible to determine from the record whether all randomized participants were included in each analysis, what exclusions occurred, or whether the analyzed groups retained their randomized assignments.

The registry identifies the trial as randomized, but does not report whether the primary analysis followed intention-to-treat, per-protocol, or another population definition. It also does not provide sensitivity analyses assessing the effect of missing data, nor does it describe handling of missing outcome observations. These gaps limit evaluation of bias from incomplete follow-up and prevent a full assessment of the robustness of the posted estimates.

The record lists no reported analyses. Details such as a prespecified statistical analysis plan, interim analyses, covariate adjustment, and multiplicity control are not reported in the registry record. Their absence from the record should not be interpreted as proof that a method was or was not used; it means the registry does not document it. The posted unadjusted comparisons can still be described, but conclusions about confirmatory testing and analysis populations should remain cautious.

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 non-serious adverse event terms

The registry reports serious adverse events as 0 affected participants in each group. For other adverse events, it records 38 affected participants among 38 at risk in the Ialuset® Application group and 44 affected participants among 44 at risk in the Bandage Skin Hydrosorb group. These are registry counts; the record does not provide the specific non-serious event terms in the posted summary.

The death counts are recorded separately as 14 in the Ialuset® group and 4 in the bandage group. The record does not state the timing, causes, relationship to treatment, or how deaths relate to the adverse-event follow-up period. These figures should not be interpreted as evidence that an application caused or prevented deaths.

Adverse-event counts need context about definitions, ascertainment, follow-up duration, severity, and attribution. The registry record does not provide those details here, and it lists no top serious adverse-event terms. The differing at-risk counts also mean that raw counts alone do not describe comparable rates without fuller information about follow-up and event reporting. The figures are a limited registry safety summary, not a complete assessment of safety.

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

The registry results describe a randomized comparison of a hydrogel bandage and Ialuset® applied to the cervical skin during radiotherapy. For the primary pain endpoint, the posted event counts and unadjusted estimate suggest a higher observed event risk in the bandage group, but the confidence interval is wide and includes values in both directions. The result does not provide a precise estimate of the group difference.

That uncertainty is important. A non-significant p-value does not establish that the applications have the same effect, and the data do not demonstrate equivalence. Conversely, the point estimate alone does not establish that the bandage leads to more pain deterioration. The interval and the limitations of the registry information should be considered together rather than relying on a single summary value.

The secondary chemotherapy dose-reduction result is also uncertain and measures a different outcome over a longer period. It does not resolve the uncertainty in the primary result. The registry’s safety summary reports no serious adverse-event participants in either group, along with other adverse-event and death counts, but does not provide details needed to attribute events or compare safety comprehensively.

In general, randomized trials can support causal interpretation when allocation, follow-up, and analysis are adequately implemented and documented. The registry confirms randomized allocation but does not report several details needed to assess those conditions, including sequence methods, missing-data handling, analysis populations, and the original statistical plan. The findings therefore support a cautious description of the posted comparisons, not a broad claim about benefit, lack of benefit, or equivalence.

The record is a source of trial information, but its posted analyses are limited. The result should be understood as an imprecise estimate based on the recorded outcome counts, with important methodological details not reported in the registry record. It does not justify medical advice for an individual or a claim that either application is effective or ineffective.

17. Why This Trial Matters Statistically

This trial illustrates why an event count alone is not enough to interpret a randomized comparison. The primary outcome uses a defined threshold for pain deterioration, and the analysis contrasts the frequency of that event between groups. The estimate, its confidence interval, and the outcome denominators each contribute different information: the counts describe what was recorded, the estimate gives the direction and size of the contrast, and the interval communicates uncertainty.

Here, the primary interval includes both negative and positive differences, so the result does not precisely establish which group had the lower event risk. That is a useful distinction between absence of strong evidence against no difference and evidence that the groups are alike. The same reasoning applies to the secondary endpoint, whose uncertainty should not be hidden by the fact that its event counts match.

The record also shows why registry transparency matters. Details about missing baseline pain ratings, participant flow, analysis populations, multiplicity, and the original statistical plan would help readers assess whether the posted summaries answer the prespecified question and how robust they are. Without these details, the statistics can be interpreted, but the full evidential context remains incomplete.

Finally, planning calculations based on an observed effect are not a retrospective measure of a trial’s success. They show how assumed effect size influences future sample-size requirements under stated assumptions. Smaller effects require more participants for a given power target. Keeping those planning illustrations separate from the observed results prevents a common misreading of power and supports more careful interpretation of uncertain clinical evidence.

18. Limitations

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

The registry record has several trial-specific gaps that limit interpretation. Although it identifies randomized allocation and no masking, it does not report the randomization sequence method, allocation concealment, or whether outcome assessors were masked. The intervention naming is also inconsistent: the bandage is identified as Hydrotac® in the intervention list and Hydrosorb® in the arm description. The record does not clarify this naming difference.

The primary endpoint depends on baseline and end-of-treatment pain ratings, yet the record notes 5 patients without a baseline answer and does not describe how this was handled. It does not report the number of missing follow-up ratings, participant flow, exclusions, or the analysis population. Outcome denominators differ between the primary and secondary summaries, and their relationship to listed enrollment is not explained.

The registry does not report the original sample-size justification, statistical analysis plan, primary test method, multiplicity strategy, interim analyses, or covariate adjustment. No reported analyses are listed. Therefore, the posted unadjusted comparisons cannot be checked against a documented prespecified analysis in the registry record. The exact confidence-interval procedure and confidence level are also not stated.

The safety summary lacks event terms and details on timing, severity, attribution, and follow-up. Death counts are listed, but causes and relationship to treatment are not reported. The record also provides limited detail on how the secondary chemotherapy dose-reduction outcome was defined or assessed during its stated timeframe. These omissions constrain assessment of both clinical interpretation and data completeness.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Impact of Applying a Bandage Skin Hydrogel on the Pains of the Head and Neck in Patients With Cancer of Head and Neck Treated With Radiotherapy — NCT01520701.
• Registry record last updated 2026-09-01; status last verified 2026-08.
• Results first posted 2026-09-01.
• 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

NCT01520701 is recorded as a completed phase 3 randomized, parallel-group trial with no masking and listed enrollment of 130. It compared Ialuset® Application with a cervical skin hydrogel bandage during radiotherapy for head and neck cancer. The bandage is named Hydrotac® in one entry and Hydrosorb® in another.

The primary endpoint was deterioration of three or more points on the EVA pain scale from baseline to the end of radiotherapy, stated as 2 months after inclusion. The posted comparison is unadjusted and imprecise, with a confidence interval spanning no difference. The registry also lists chemotherapy dose reduction during 36 months after radiotherapy and a limited adverse-event summary.

Important details—including missing-data handling, analysis populations, the original sample-size rationale, and multiplicity methods—are not reported in the registry record. The posted results are best read as uncertain summaries rather than definitive evidence of a difference or equivalence.