Welcome back to the journal review. This is the February twenty twenty-six issue of the Journal of the American Academy of Dermatology, and we've got four pieces worth your attention this month — three are correspondence, letters to the editor responding to recently published work, and one is a genuine brief report with new retrospective data. Let's get into it.

First up, a letter responding to Hong and colleagues' phase three randomized trial comparing radiotherapy against imiquimod for complex lentigo maligna. You'll recall the original trial itself was a head-to-head comparison of these two non-surgical options in a population where surgery isn't the first choice — typically because of anatomic location, size, or patient factors on the face. This letter from Chen and Chen doesn't challenge the trial's overall design, but does a deeper dive into supplementary data the original authors didn't emphasize, specifically around reflectance confocal microscopy, or R-C-M, findings at baseline.

The core point is this: when they broke down failure rates by confocal morphology, patients whose baseline R-C-M showed round atypical cells at the dermo-epidermal junction had a dramatically higher failure rate after radiotherapy compared with imiquimod — about twenty-seven percent versus seven percent, a roughly five-fold increase in odds, and this was statistically significant. A similar pattern held for large atypical junctional cells, again around a four-fold increase in radiotherapy failure risk, also significant. So the implication the letter writers draw is that R-C-M isn't just a diagnostic adjunct here — it may actually predict which patients will fail radiotherapy, and could be used to steer higher-risk confocal phenotypes toward imiquimod instead.

Second point, and this is important methodologically: R-C-M wasn't used equally in both arms of the original trial — it was performed in about ninety percent of the radiotherapy group but only seventy-seven percent of the imiquimod group. That's a real detection bias concern. Interestingly, among patients who never got R-C-M assessment, radiotherapy failures were essentially absent — though numbers were small — which raises the possibility that more intensive imaging in the radiotherapy arm simply caught more subclinical failures, inflating that arm's apparent failure rate rather than reflecting a true treatment difference.

Third, there's a timing story buried in the data. Early failure rates at six months were similar between the two treatments, around five percent each. But between six and twenty-four months, radiotherapy failures kept accumulating while imiquimod's didn't, so by two years the radiotherapy failure rate was roughly double that of imiquimod — about twenty-one percent versus ten percent. The letter's message here is that short follow-up will systematically underestimate radiotherapy's recurrence risk in an indolent disease like this, and surveillance needs to extend well past the one-year mark.

They also flag that acute skin toxicity was worse with radiotherapy at three and nine months, clinically meaningful even where statistical significance didn't hold after adjustment, and — notably — only the radiotherapy arm underwent systematic late-toxicity assessment, where fibrosis, telangiectasia, hypopigmentation, and atrophy affected up to half of patients by two years. Imiquimod's long-term toxicity profile simply wasn't captured in parallel, so any safety comparison between the two arms is inherently lopsided.

Bottom line from this letter: the trial is valuable, but the real actionable nugget is that confocal morphology, particularly round atypical junctional cells, may help pre-select patients for imiquimod over radiotherapy, and that anyone using radiotherotherapy for lentigo maligna needs a longer surveillance horizon than early trial data would suggest. This is provocative and worth watching, but it's a secondary, likely underpowered subgroup analysis — interesting hypothesis-generating signal, not yet a practice mandate.

Moving to our second letter, this one responding to Joshi and MacFarlane's study on in situ extramammary Paget disease, or E-M-P-D, in the United States. The original study characterized epidemiology and prognosis of the in situ form specifically. This response from Li and Long raises three clarifying questions.

First, the original study found that seventy-nine percent of in situ E-M-P-D cases were vulvar, compared with roughly half of invasive cases. The authors of the original paper suggested tissue-sparing approaches like Mohs might be preferable for vulvar disease, but didn't break down actual surgical techniques or outcomes used in their cohort. The letter writers point to outside literature showing conventional wide surgical excision for E-M-P-D carries a recurrence rate around thirty-seven percent, whereas Mohs micrographic surgery achieves cure rates in the high nineties — ninety-eight percent for primary disease, ninety-six percent for recurrent disease. Their ask is straightforward: future analyses should stratify by surgical technique, radical versus tissue-sparing, to actually justify the tissue-sparing recommendation with outcome data rather than inference.

Second, the original study identified socioeconomic factors — income, marital status — as associated with delayed diagnosis, but didn't explore why. The letter appropriately notes this could reflect health care access, patient awareness, or provider diagnostic thresholds, and that distinguishing between these would actually let you design an intervention rather than just document a disparity.

Third, and this is the most clinically interesting point, age over seventy showed only a non-significant trend toward worse disease-specific survival in situ disease — hazard ratio around two, but with a confidence interval crossing one — whereas that same age cutoff was a clear, significant risk factor for invasive disease. The letter writers suggest this divergence might reflect differences in comorbidity burden or treatment tolerance in older patients with early-stage disease, though this remains speculative pending further work.

Overall, this is a constructive letter asking for more granularity rather than disputing the original findings — nothing here changes practice today, but it reinforces what most of us already do: favor Mohs for vulvar E-M-P-D given the substantial cure-rate advantage over conventional excision, even though this particular paper didn't generate that comparison itself.

Third piece is a response letter engaging with Thakker and colleagues' article on ethical deployment of artificial intelligence in low-resource dermatology settings. This is less about new data and more a framework discussion, so I'll walk it through as the commentary it is rather than force a results-and-limitations structure onto it.

The authors agree with the original piece's premise — AI as adjunct, not replacement — but argue the original article's emphasis on performance stability doesn't go far enough. They introduce the FUTURE-AI checklist, a consensus framework built around six dimensions: fairness, meaning consistent performance across different skin types and populations; universality, meaning generalizability to new clinical settings without requiring in-house AI expertise; traceability, meaning the tool's performance is documented and monitored across its entire lifecycle; usability, meaning end users are involved in the design process from the start; robustness, meaning performance holds up in real-world practice, not just in validation datasets; and explainability, meaning the tool can show clinicians why it reached a given conclusion — through heatmaps highlighting relevant image regions, or confidence scores, for instance.

Their argument is that explainability is the piece most likely to get short-changed, and it matters practically, not just philosophically — in Europe it's now a regulatory requirement that any clinician using an AI system be able to validate its decision, which is difficult when the underlying model, especially something like a large language model, is fundamentally a probabilistic black box generating multiple hypotheses simultaneously. Their point is that this creates a real educational obligation: clinicians need targeted training in how to interpret AI outputs, not just how to operate the software, and they suggest medical curricula should incorporate evidence-based-medicine-style courses on AI, ideally co-taught with engineers.

On the regulatory side, they advocate for certifying AI diagnostic tools the way we certify drugs — through randomized controlled trials — and for streamlining recertification, since current frameworks tend to lock in a validation at launch and discourage iterative updates for fear of restarting the entire certification process. They close by flagging that recent U-S federal AI policy discussions around open-source models and interpretability may shape how this plays out going forward.

Nothing actionable for tomorrow's clinic here, but conceptually important if your practice is evaluating or piloting any AI-assisted diagnostic tool — the FUTURE-AI framework is a genuinely useful checklist to hold up against any vendor's marketing claims before you adopt something.

Now to the one true original data piece this issue — a brief report examining skin cancer risk in bone-marrow transplant patients treated with ruxolitinib compared with other immunosuppressive therapies. Ruxolitinib, for context, is a Janus kinase inhibitor increasingly used for refractory graft-versus-host disease after bone-marrow transplant. We already know transplant recipients on immunosuppression carry elevated skin cancer risk generally, but ruxolitinib is new enough that its specific contribution to that risk hadn't been well characterized — that's the gap this paper addresses.

Methodologically, this is a retrospective cohort study built on the TriNetX research database, which aggregates de-identified records across over a hundred health care organizations. They identified patients with a bone-marrow transplant code who were subsequently exposed to ruxolitinib, and compared them against a control cohort exposed to any other immunosuppressive medication post-transplant, excluding ruxolitinib. Anyone with a prior history of skin cancer before transplant was excluded, and the two cohorts were propensity-matched on age, gender, race, ethnicity, and underlying hematologic malignancy. Outcomes were captured via diagnostic codes for squamous cell carcinoma, basal cell carcinoma, melanoma, and carcinoma in situ, analyzed with odds ratios and Kaplan-Meier time-to-event curves.

Why a retrospective database design rather than a trial? The authors don't spell this out explicitly, but it's the obvious choice here — this is a rare-ish, long-latency outcome in a fairly narrow population, and a database like TriNetX gives you the numbers and years of follow-up you'd never get from a prospective single-center study, especially for a drug this new. The tradeoff, as always with claims-based data, is that you're relying on diagnostic codes rather than confirmed pathology, and residual confounding from unmeasured variables like sun exposure, skin type, or cumulative immunosuppressive dosing can't be fully addressed by propensity matching on demographics alone.

Onto results. About five thousand patients total, split evenly, twenty-four seventy-four in each arm, well matched on age — averaging around fifty-three in both groups — and similar across gender, race, and ethnicity. The headline finding: ruxolitinib exposure was associated with a significant increase in both squamous cell carcinoma and carcinoma in situ — roughly a seventy percent increase in the odds of squamous cell carcinoma, and closer to a nearly two-fold increase in the odds of carcinoma in situ, both clearly significant and clinically meaningful given how directly this should inform surveillance intensity.

Basal cell carcinoma showed no meaningful difference — odds were essentially equivalent between groups, and the Kaplan-Meier curves looked similar over a twenty-year window.

Melanoma is the curious one: the odds ratio actually favored ruxolitinib, showing a significant reduction in melanoma odds, roughly a forty percent lower likelihood. But when they ran the time-to-event log-rank comparison, there was no significant difference in melanoma incidence over time between the groups. So you have a significant point-estimate reduction that doesn't hold up under a different, arguably more robust analytic lens — the authors appropriately don't over-interpret this, and neither should we. This is exactly the kind of situation where a single significant p-value shouldn't be taken as durable evidence of a protective effect; it's more likely a statistical artifact of follow-up asymmetry between the cohorts than a true biological signal.

Which brings us to the major limitation, and it's a substantial one: follow-up duration was meaningfully shorter in the ruxolitinib cohort than in controls, given the drug's relative novelty — capped well under thirteen years in the ruxolitinib group versus close to nineteen years in controls. Since we know cutaneous malignancy risk after bone-marrow transplant has a documented lag time stretching anywhere from seven to twenty-seven years post-transplant, the ruxolitinib cohort simply hasn't had time to fully mature. That means the true long-term risk, particularly for basal cell carcinoma and melanoma where longer latency may matter more, could still be underestimated here.

Practical takeaway: this doesn't change the fundamental recommendation that all post-transplant, immunosuppressed patients need routine dermatologic surveillance — that's already standard. What it does add is a specific signal that ruxolitinib-exposed patients may warrant heightened suspicion for squamous cell carcinoma and carcinoma in situ specifically, supporting a lower threshold for biopsy and closer interval follow-up in this subgroup. The melanoma and basal cell carcinoma findings are not actionable yet — call them hypothesis-generating at best, given the discordant statistical signals and immature follow-up. This is a good one to flag for your own transplant-dermatology collaborations, but not yet grounds for a formal protocol change beyond what you're likely already doing.

That wraps our four pieces this month — a confocal-microscopy-driven challenge to how we interpret lentigo maligna trial data, a call for more granular surgical outcome reporting in extramammary Paget disease, a practical framework for vetting AI tools before you trust them clinically, and new real-world evidence sharpening our surveillance priorities in ruxolitinib-treated transplant patients. Thanks for listening, and we'll see you next month.