onc brain

At median follow-up 60 mo: 5-yr BCR-FS 44%, 5-yr MFS 71%, 5-yr CSS 92%. No per-arm, per-subgroup, or comparator figures reported in source.

Beyond the missing design, the source names no treatment received, so the 44% biochemical failure rate cannot be read as a benchmark for any specific perioperative strategy. No N, no risk-stratification criteria, and no confidence intervals accompany the three rates.

Source gives three 5-yr rates and follow-up only. No design, N, treatment, or comparator, so no SOC read is supportable.

A point-counterpoint conference presentation, arguing the negative position. The evidence marshalled is three published studies: a prospective single-arm imaging trial (n=16 evaluable), a bipolar androgen therapy series (n=6), and the RECIP 1.0 framework paper.

The anchor trial enrolled pts with APMR starting abiraterone or enzalutamide, imaged with 18F-DCFPyL PET/CT immediately before therapy and again at 2-4 months. The BAT series imaged at baseline and 3 months.

Prognostic separation was consistent across both quantitative stratifiers, with DPSM HR 5.03 (95% CI 1.17-21.65) and DASM HR 9.31 (95% CI 1.81-47.87) for overall survival. A mixed but predominantly increased uptake pattern marked the shorter time to therapy change.

RECIP 1.0 is the field's standardization attempt, categorizing PD/PR/SD/CR by combining PSMA PET with CT, but it was derived in the radioligand therapy setting and its transfer to AR-directed therapy is exactly what Rowe argues is unestablished.

Beyond the small samples, the measurement layer itself is unvalidated: repeatability work using Bland-Altman, ICC, and within-subject coefficient of variation found lesion identification and segmentation variability material even above 1.5 cm³. A biomarker whose test-retest behaviour is uncertain cannot support a serial-change decision rule.

The talk separates two claims that often get merged: that post-therapy PSMA PET change is prognostic, which the data support, and that it is a valid response assessment, which requires reproducibility and a therapy-independent relationship between uptake and burden. Prognostic value in a 16-patient series does not license per-patient treatment decisions.

Conference position talk, not a result. Its supporting datasets are n=16 and n=6 prospective series; no comparative design establishes or refutes PET response assessment.

Prospective observational analysis within the Michigan Radiation Oncology Quality Consortium (MROQC), a statewide quality collaborative. 26 centers, accrual June 2020 to November 2024, N=553. Intended ADT duration and ARPI use were collected prospectively at the treatment decision, not abstracted retrospectively.

Intact (non-postoperative) high-risk M0/N0-1 prostate cancer planned for definitive radiotherapy. Risk features: cT3/4 13.3%, cN1 19.9%, GG 4-5 75.0%, PSA ≥20 ng/mL 40.0%.

Primary outcome was intended guideline-concordant ADT (GC-ADT, ≥18 months) per the 2022 AUA/ASTRO recommendation of 18-36 months. Secondary analyses covered multivariable predictors of GC-ADT, ARPI adoption before versus after STAMPEDE M0 publication, and facility-level variability via a mixed-effects model with treatment site as random intercept.

91.3% were recommended ADT and 67.0% were guideline-concordant. Among the 27.9% meeting STAMPEDE M0 eligibility, ARPI recommendation went from 0% pre-publication to 23.2% after. Site-level variability remained significant on multivariable analysis (P<.0001).

The 2022 AUA/ASTRO guideline sets 18-36 months, and STAMPEDE M0 supports ARPI intensification for ≥2 of cT3/T4, GG 4-5, PSA ≥40, or cN1. Both benchmarks are met by a minority here, echoing the long-standing gap between the long-course ADT durations tested in EORTC 22863 and RTOG 9202 era trials and what is actually intended in practice.

Intended duration is a proxy for delivered duration, so the true concordance rate could fall further with early discontinuation. STAMPEDE M0 eligibility was applied to a cohort accrued partly before that trial reported, so the 23.2% post-publication figure reflects an adoption curve still in motion rather than a steady state.

The finding that facility explains variance after adjusting for cN1, grade group, and PSA is the load-bearing result: with case mix accounted for, where a man is treated still moves how long he is recommended ADT. That is a quality-improvement target rather than an evidence gap, and it is the kind of signal a consortium is uniquely built to detect and act on.

Prospective practice-pattern survey of intended treatment, no efficacy endpoint. Documents a care-delivery gap rather than testing whether the guideline duration is right.

MFS event ascertainment was PSMA PET-dominant: 53.0% of distant metastases in the apalutamide group and 60.7% in the comparator were identified by PET rather than conventional imaging. EFS is named in the thread, but no effect size for either endpoint appears in the source.

The contested question is whether a PET-detected metastasis is the same event MFS was built to count. A commentator's hypothetical, explicitly not trial data, models 100 pts per arm with 60 BCRs on ADT alone and 50 on apalutamide plus ADT to show how differential detection alone can widen an apparent gap.

The NEJM sentence quoted in the thread is truncated, so the 60.7% figure's arm label is inferred from a two-arm comparison rather than read directly. The full presentation has not occurred, and the source gives no phase, N, follow-up, or eligibility.

Results online but the source thread carries no EFS or MFS effect size, so no strength bucket is defensible; ascertainment concern noted, not adjudicated.

Not reported in source. The tweet gives a 5-year local control figure with no study type, N, institution, or registry identifier, so design cannot be inferred.

SBRT to primary RCC; dose, fractionation, number of fractions, and target definition are not reported in source. These are the parameters that gate transfer to practice, and none are available here.

100% local control at 5 years as stated in the source tweet. No confidence interval, no n-at-risk, and no statement of whether this is a Kaplan-Meier estimate or a crude proportion.

Beyond the missing design, the specific risk is effective follow-up: a medically inoperable RCC cohort loses pts to non-cancer death well before 5y, so a 100% figure can rest on very few pts at risk. Local control definition (RECIST-style size change vs absence of growth vs biopsy) is also unstated and swings the estimate.

Single tweet with one number, no N, design, dose, or LC definition. Cannot judge whether the 100% figure reflects efficacy or short effective follow-up.

Two de-escalation levers reported in source: contralateral neck sparing in a specified subgroup, and reduction of the primary CTV dose to 56 Gy. Fractionation, technique, and the dose to involved or high-risk volumes are not stated in the source text.

Described as a trial, but phase, randomisation, N, sites, and follow-up are not stated in the source tweet.

No primary endpoint, effect size, or toxicity result reported in source. The tweet is commentary on the trial's approach, not its results.

Everything that would let a reader act on this is missing from the source: the selection rule for contralateral neck omission, the comparator, and any locoregional control or late-toxicity figures. A de-escalation result is only interpretable against its non-inferiority margin, which is not given.

Source is a single commentary tweet with no design, N, endpoint, or effect size. Nothing to classify beyond the de-escalation concept.