BICR in Oncology Trials: What Registry Wording and FDA/EMA Evidence Can Tell You

The decision starts with the endpoint

An independent review plan should follow the endpoint, the risk of biased assessment and the data that will remain available after local progression. Public registration patterns can help a team find relevant precedents. Choosing blinded independent central review (BICR) requires study-specific scientific and operational evidence.

Our audit of the 1 August 2026 AACT snapshot identified 22,772 interventional studies with registered start years 2010 through 2025, a phase 2, phase 2/3 or phase 3 designation, and a Neoplasms index term. A broad search of their outcome text matched review-related language in 1,794 studies, or 7.9%. A more explicit dictionary matched 1,441, or 6.3%. These are phrase-screen results, not confirmed BICR adoption rates. The cohort includes cancer-related supportive-care research, and some matched assessments concern pathology or laboratory values rather than scans. [1]

The distinction changes the headline in the subset most relevant to a sponsor planning a confirmatory oncology study. Among 1,177 industry-sponsored phase 3 studies with tumour-assessment wording in a primary outcome, 714 matched the broad review dictionary somewhere in their outcomes. Requiring explicit independent-review language reduced that count to 650. Requiring the explicit language to appear in the same tumour-primary outcome reduced it again to 579: 60.7%, 55.2% and 49.2%, respectively. A claim that “most comparable trials use BICR for their primary endpoint” therefore goes beyond this evidence. [1]

FDA and EMA guidance provide a firmer basis for the decision. They discuss complete review, investigator assessment and prospective audit strategies in relation to study design and potential bias. The appropriate scope and audit method depend on the study; a universal hazard-ratio cutoff, audit percentage or cost threshold is unsupported. The practical output is a documented review strategy, agreed before results can influence it, with a clear place in the protocol and analysis plan. [2][3]

This report combines the registry audit, the relevant regulatory texts and eight methodological or comparative studies. Its final sections turn that evidence into questions for an imaging charter and a review-model decision. The accompanying chart-data workbook contains all plotted values and their provenance.

What the registry screen actually measures

AACT represents ClinicalTrials.gov records as relational tables. We joined study metadata, indexed conditions, lead sponsors, designs, countries and registered outcomes. A study entered this analysis through its registered phase, start year and Neoplasms indexing, irrespective of recruitment status or whether its start date was estimated. Country flags used non-removed country entries. This is an operationally defined registry cohort, not an adjudicated census of therapeutic oncology trials. [1][4]

The outcome scan covered 160,792 rows. Review phrases were searched in outcome measures and full descriptions. The broad screen combined BICR-related expressions, independent committee or facility wording, bare IRC/IRF acronyms, and general central-assessment language. The narrower screen retained BICR/BIRC and explicit independent or blinded review expressions while removing the bare IRC/IRF alternatives and the general-central branch. Implementation would require confirmation from protocol and operational evidence. [1]

That refinement matters because acronyms and central assessment are ambiguous. In NCT03710564, IRF denotes intraretinal fluid. Other positive records concern centrally assessed Ki67, pathological complete response or review of infection outcomes. Even explicit BICR can include bone-marrow pathology, while an independent committee applying myeloma criteria may use laboratory information. These examples explain why “independent imaging review” would be an inaccurate name for the whole screen. [1]

The broad screen contained 353 studies outside the narrower definition, 19.7% of its positives. That is a sensitivity comparison, not an estimate that 19.7% were false positives. There has been no full-cohort manual adjudication to estimate precision or recall. Negative records may omit the review arrangement or describe it in wording the dictionary misses. A registry entry also need not contain an imaging charter or the current operational plan. [1][4]

A separate tumour-related dictionary identified progression, response, disease-free or event-free survival, and named assessment criteria, among other terms. For that flag we searched the measure and the first 300 description characters. “Tumour-primary” therefore means a registered primary-outcome row matched that dictionary; it is not a clinical adjudication that all aspects of the endpoint are imaging based. “Same primary” adds the requirement that review wording and tumour wording occur in that same row. [1]

Across all sponsors, explicit wording rose from 583 of 16,883 phase 2 records, or 3.5%, to 792 of 5,003 phase 3 records, or 15.8%. The corresponding broad results were 4.8% and 17.9%. Phase 2/3 sat between them. The consistent phase gradient describes disclosure patterns; review scope, quality, cost and motivation remain unmeasured. [1]

The year chart retains every year for all three series, including non-industry studies. Each point describes the studies assigned that registered start year as seen in the same August 2026 snapshot. Older entries may have been amended, so the series describes historical start-year groups through their current records. Changes can reflect the mix of registered studies, the language used in records, reporting completeness and genuine changes in design. Separating these explanations would require additional evidence. [1]

Industry sponsorship is associated with more review wording. The explicit screen matched 1,264 of 5,526 industry-led studies, or 22.9%; the broad screen matched 26.3%. The lead-sponsor class is the registry's agency classification. OTHER combines several kinds of sponsor. Industry-led status follows the lead sponsor, with collaborators recorded separately. [1]

These comparisons are useful for constructing a protocol-review sample. Questions about purchasing motivation, investment adequacy or filing outcomes would need budget, procurement and regulatory-interaction evidence beyond these records.

Masking and country comparisons need narrower claims

An apparently surprising association survives the more explicit dictionary. Among industry studies with tumour-primary wording, explicit review language appeared somewhere in the outcomes of 822 of 2,534 open-label studies, or 32.4%, and 322 of 796 studies with any masking, or 40.5%. When review language had to match the same tumour-primary row, those rates were 29.2% and 32.8%. [1]

“Any masking” includes single, double, triple and quadruple categories. The category can cover different masked roles; treatment effects or adverse events may still reveal assignment to an assessor. The comparison is unadjusted for phase, endpoint, disease, year and other design characteristics. The observed association leaves the role of bias risk unresolved. FDA's imaging guidance and EMA's discussion of treatment-related clues both make the actual information available to assessors a study-specific question. [3][5]

The country comparison has similar limits. Among industry phase 3 studies, explicit review wording appeared in 434 of 944 records listing China, or 46.0%, versus 308 of 1,284 without China, or 24.0%. The broad screen would instead produce 50.6% and 27.2%. The comparison is limited to the China-listing flag. Sponsor nationality, regulatory destination and actual recruitment require separate evidence. [1]

A useful next step for a study team is to inspect a small set of genuinely comparable protocols and their public documents: similar disease, line of therapy, endpoint, masking feasibility and development objective. Country and phase can help find that set. Use the resulting set to examine those protocol-level details.

The three-layer comparison in the figure is also a reporting discipline. A trial-level statement can mean that two features occur somewhere in the same study. An endpoint-level statement requires linking them to the same outcome. A statement about actual execution requires evidence beyond the registration record. Keeping these levels separate avoids giving a procurement team a precise percentage attached to the wrong question.

What FDA and EMA support

FDA's December 2018 oncology-endpoints guidance addresses independent assessment in the context of potentially subjective endpoints and assessment bias. It allows that BICR may not be necessary in some adequately blinded randomized settings, and discusses a prespecified random audit as an alternative in appropriate circumstances. It also advises seeking FDA input on an audit strategy. This is conditional guidance, not a general exemption for any study labelled double-blind. [2]

EMA's PFS/DFS appendix gives the most direct discussion of complete review and audit. It recommends complete BICR where important investigator bias is expected or the expected treatment effect is moderate. An audit approach needs prospective sampling and decision rules capable of addressing directional discordance, with case-specific regulatory advice before implementation. If important bias cannot be excluded, escalation to complete review may be necessary. [3]

The broader EMA anticancer guideline also relates external review to the objectives of the trial. Exploratory objectives can also justify external review. Endpoint acquisition and follow-up remain important whichever review model is selected. The assessment method must fit the scientific question, disease and intended use of the evidence. [6]

One limitation is especially important for PFS. If local progression leads a participant to leave protocol follow-up, later central review may lack scans that would have been collected had the central reader's assessment governed follow-up. This can create informative censoring. Independent readers cannot reconstruct observations that were never acquired. Real-time review or additional follow-up after local progression can be relevant design options, subject to feasibility and the protocol. [3][7]

Three decisions consequently need to be made together:

• The assessment decision: who determines progression or response, under which criteria and with what information?
• The follow-up decision: which events stop scans or other assessments, and what continues after local progression or treatment discontinuation?
• The analysis decision: which assessment drives the primary analysis, and how are discrepancies, missing data and censoring handled?

These questions are an editorial synthesis of the guidance and methods literature. They organize the study-specific design discussion. Their value is that a review model can look sound in isolation while depending on an acquisition schedule or censoring rule that defeats its purpose.

FDA's imaging-process guidance adds operational detail: acquisition consistency, image quality, reader qualification and training, presentation methods, clinical-information access and adjudication. The appropriate amount of clinical information depends on the disease and assessment method. “Blinded” should therefore be implemented as a defined information boundary, rather than a blanket claim that readers must receive no clinical data at all. [5]

Similarly, specifying a charter before the study and submitting it to FDA are distinct actions. The applicable guidance and the study's regulatory interactions should determine what is submitted and when. Reader arrangements, adjudication methods and any audit fraction should be justified for the particular study. [2][5]

Agreement studies answer several different questions

Eight publications help explain why central and investigator assessments can be both strongly correlated and meaningfully different. Their units include individual patients, treatment-effect estimates and statistical conclusions. Potential population overlap has not been deduplicated, so we retain each publication as a separate evidence unit.

Dodd and colleagues examined the methodological problem of informative censoring, including a real randomized phase 2 example. Amit and colleagues combined a meta-analysis of 27 randomized phase 3 trials with simulation work; their correlation of treatment-effect estimates was 0.947. These papers support thinking carefully about when and how review can verify local results, rather than assuming that universal full review is the only scientifically defensible design. [7][8]

Zhang and colleagues reviewed 76 trials involving 45,688 patients. Seventeen trials had inconsistent statistical inferences for ORR, PFS and/or time to progression. The resulting 22.4% describes discordance across those reported metrics in this evidence set. The pooled PFS comparison used 72 trials and the pooled ORR comparison used 29. [9]

Dello Russo and colleagues reported 32 PFS estimates from 28 trials, with a pooled investigator-to-BICR hazard-ratio ratio of 0.98. Jacobs and colleagues examined 24 metastatic breast cancer trials and reported a discrepancy index of 0.97 and an intraclass correlation of 0.831. These are comparisons of relative treatment effects in selected evidence sets. Patient-level agreement and applicability to a new indication need their own evidence. [10][11]

The Roche-trial analysis by Lian and colleagues needs particular care. Table 2 reports an overall BICR-to-local-evaluation hazard-ratio ratio of 1.044, with a 95% confidence interval of 1.009 to 1.081, across 55 PFS comparisons. The double-blind subset was 1.014 (0.958 to 1.073); the open-label subset was 1.062 (1.016 to 1.110). The overall and open-label intervals excluded one. High agreement therefore coexisted with a small average difference in relative treatment-effect estimates. [12]

Its often-quoted 87% agreement has another denominator: 40 of 46 PFS comparisons with alpha-controlled statistical testing. Its relevance to a regulatory decision depends on the endpoint and the rest of the benefit-risk evidence. [12]

Tang and colleagues studied 70 hematology-oncology trials. Their pooled PFS ratio of 0.96 (0.89 to 1.03) used 35 comparisons and runs in the opposite direction, investigator divided by BICR. The reported perfect agreement in statistical significance applied to 33 primary-PFS comparisons. Comparing the ratios on one scale requires inversion, while retaining their population and endpoint differences. [13]

VELIA offers a concrete illustration. Investigator-assessed median PFS was 23.5 versus 17.3 months, with a hazard ratio of 0.683. The supplementary BICR analysis reported 29.3 versus 19.2 months and a hazard ratio of 0.637. The relative effects were consistent despite different medians; the BICR comparison was supplementary, without an alpha-controlled test. Describing this as identical measurements or an independently identical regulatory conclusion would overstate the paper. [14]

For planning, separate four questions when reading an agreement study: did readers assign the same status to the same patient; did they date progression similarly; did they estimate similar between-arm effects; and did they reach the same prespecified statistical inference? Each question needs the relevant measure of agreement. The relevant question depends on what the study needs its independent review to verify.

A review-model discussion and charter checklist

The following table is a planning aid. It organizes evidence for regulatory discussion; sampling and review scope remain study-specific choices.

For a proposed audit, the important deliverable is a prospective method. Explain how participants or assessments enter the sample, which discrepancies are measured, how directional bias will be assessed, and what result triggers broader review. The reviewed guidance provides no universal percentage that can simply be inserted into every charter. Operating characteristics need to fit the endpoint, expected event information and planned analysis. [2][3]

For complete BICR, the useful work starts before images reach a reader. The charter, protocol and analysis plan need to describe compatible versions of the same process. The checklist below is our implementation synthesis of the regulatory and methodological sources, not a claim that every item is a separately mandated document. [2][3][5]

RECIST 1.1 is one widely used response framework. A charter still needs the operational choices that connect the criteria to this study's images and endpoint. Disease-specific criteria and modifications should be identified explicitly rather than hidden inside a generic “RECIST-compliant” label. [15]

FDA's NSCLC-endpoints appendix gives a useful example of the detail behind tumour measurement and data collection. Teams can use it to check whether the source observations needed for their chosen assessment are actually collected and retained. Adapt its disease-specific recommendations to the intended assessment. [16]

A study team can make this checklist reviewable by walking through a few representative cases before finalizing the process: an unevaluable baseline scan, local progression without central confirmation, a late scan and a disagreement that reaches adjudication. Those are proposed implementation exercises, not regulator-prescribed test cases. Each should expose which person acts, which data are available and which controlled rule determines the next step.

The same discipline applies to change. A new imaging modality, revised criterion or changed follow-up rule can affect readers, data transfer and the analysis together. Record which documents and workflows change, the effective version and how previously collected assessments are handled. A software audit trail can help preserve actions; methodological appropriateness remains a scientific judgment.

EClinCloud's IRC offering describes independent-review workflows and services. It is relevant after the sponsor has defined the endpoint and review strategy. Product availability is not evidence that a particular review model is scientifically appropriate or that a study will receive regulatory acceptance. [17]

How to use and update this analysis

The registry screen is best used to identify examples for closer review and to improve the wording of portfolio-level questions. Procurement, quality assessment and regulatory strategy require the additional evidence described above. The comparative literature supports examining both relative effects and patient-level discrepancies, with study-specific interpretation of their importance.

To update the registry analysis, retain the snapshot date, cohort definition, dictionary version and the distinction between any-outcome and same-primary matches. Report changes in these definitions separately from changes in the counts. A broader synonym list may improve recall while creating new false positives. A smaller, clinically adjudicated protocol sample could build on this screen to examine actual review arrangements.

For an individual study, the decision is ready for review when the team can explain the proposed endpoint assessment, the plausible sources of bias, the follow-up and missing-data implications, and the evidence supporting the selected review scope. That explanation is more useful than a claim that BICR is standard because a registry percentage crosses 50%.

Sources

1. EClinCloud original analysis of Clinical Trials Transformation Initiative AACT downloads, snapshot 1 August 2026, independently recomputed 6 September 2026. Neoplasms-indexed interventional phase 2, phase 2/3 and phase 3 studies with registered start years 2010-2025; 22,772 studies and 160,792 outcome rows. Broad and explicit phrase screens are not manually validated adoption estimates.

2. U.S. FDA, Clinical Trial Endpoints for the Approval of Cancer Drugs and Biologics, final guidance, December 2018.

3. EMA, Appendix 1: Methodological consideration for using progression-free survival or disease-free survival in confirmatory trials, adopted 13 December 2012, effective 1 July 2013, particularly the BICR discussion on pages 6-7.

4. ClinicalTrials.gov, Protocol Registration Data Element Definitions, accessed 6 September 2026.

5. U.S. FDA, Clinical Trial Imaging Endpoint Process Standards, final guidance, April 2018.

6. EMA, Guideline on the clinical evaluation of anticancer medicinal products, Revision 6, adopted 18 November 2023.

7. Dodd LE et al., Blinded independent central review of progression-free survival in phase III clinical trials: important design element or unnecessary expense?, Journal of Clinical Oncology, 2008. Original abstract used for the methodological summary.

8. Amit O et al., Blinded independent central review of progression in cancer clinical trials: results from a meta-analysis, European Journal of Cancer, 2011. Original abstract used for the reported cohort and correlation.

9. Zhang J et al., Systematic bias between blinded independent central review and local assessment, BMJ Open, 2018;8:e017240. Full text reviewed.

10. Dello Russo C et al., A comparison between the assessments of progression-free survival by local investigators versus blinded independent central reviews in phase III oncology trials, European Journal of Clinical Pharmacology, 2020. Original abstract reviewed.

11. Jacobs F et al., Progression-free survival assessment by local investigators versus blinded independent central review in metastatic breast cancer, European Journal of Cancer, 2024;196:113478. Original abstract reviewed.

12. Lian Q et al., Meta-Analysis of 49 Roche Oncology Trials Comparing BICR and Local Evaluation, The Oncologist, 2024. Full-text Tables 2 and 4 govern subgroup estimates and inference denominators.

13. Tang X et al., Concordance in assessments between investigators and BICR in hematology oncology clinical trials, The Oncologist, 11 November 2025. Full text reviewed; ratio direction and comparison-specific denominators retained.

14. Aghajanian C et al., Progression-free survival by investigator versus BICR: VELIA/GOG-3005, Gynecologic Oncology, 2021. Full text reviewed through the author's institutional repository.

15. Eisenhauer EA et al., New response evaluation criteria in solid tumours: revised RECIST guideline, version 1.1, European Journal of Cancer, 2009.

16. U.S. FDA, Clinical Trial Endpoints for the Approval of Non-Small Cell Lung Cancer Drugs and Biologics, final guidance, April 2015, Appendix A.

17. EClinCloud, Independent Review Committee / IRC, current company product page, accessed 6 September 2026. Describes the offering; not independent evidence of clinical or regulatory outcomes.