Welcome back to the journal review. This is your run-through of the November twenty twenty-six issue of the Journal of the American Academy of Dermatology, and we've got four pieces on deck today — two letters to the editor engaging with recent publications, and two original data reports, one a cohort study and one a real-world database study. Let's get into it. First up is a letter to the editor, responding to an earlier editorial on evidence synthesis methodology. This one is about artificial intelligence creeping into how we write systematic reviews, and honestly, it's worth your attention even if you've never touched a large language model, because residents and co-authors on your next review article probably already have. The authors' core argument is that AI tools are now woven into review workflows — drafting, screening, summarization, even risk-of-bias assessment — and that this is happening quietly, without consistent disclosure. They walk through a spectrum of tools: general-purpose large language models like ChatGPT or Claude, which are fast and flexible but prone to fabricating or misstating citations; retrieval-augmented research assistants like Elicit or Consensus, which link outputs to actual source papers and so are somewhat more trustworthy but still not immune to misinterpretation; and then the more established systematic-review management platforms and machine-learning-assisted screening tools, which the authors consider more auditable because they're built specifically for the review workflow rather than general conversation. The cautionary data point they cite is striking — when ChatGPT-4o was asked to apply the Cochrane Risk of Bias 2 tool to a set of one hundred randomized trials, it never once rated a trial as overall high risk of bias, and it agreed poorly with human reviewers. That's a meaningful finding for anyone leaning on these tools to do methodological heavy lifting, because risk-of-bias judgments directly shape a review's conclusions. The practical contribution here is a reporting framework comparison. PRISMA twenty-twenty is the baseline everyone already uses, but it says nothing about AI. PRISMA-AI is for when an AI tool is the actual subject being evaluated — think a review of a diagnostic algorithm. Neither of those covers the increasingly common scenario of AI being used as a methodological assistant during the conduct of the review itself. For that gap, the authors point to a newly proposed checklist called PRISMA-trAIce, fourteen items covering which AI tool was used, what version, what prompts, how humans and the AI interacted, and how performance was checked. It's early-stage, not yet broadly validated or formally incorporated into PRISMA guidance, but the authors argue dermatology journals should start asking for this kind of disclosure now rather than waiting for consensus. There's no methods or results section here in the traditional sense — this is an opinion letter — but the takeaway for anyone writing or peer-reviewing a systematic review is concrete: if AI touched your screening, extraction, or risk-of-bias assessment, say so explicitly, and keep a human in the loop for every judgment call. Next, a brief report — a cohort study looking at skin cancer risk in patients with systemic sclerosis who've undergone organ transplantation. The background here is that systemic sclerosis itself carries some elevated cancer risk, including nonmelanoma skin cancer, but nobody had really teased apart how much of that risk might be driven specifically by transplantation and its associated immunosuppression, as opposed to the sclerosis itself. Methodologically, this is a retrospective registry study out of Mass General Brigham, spanning over four decades. They identified patients with systemic sclerosis who had a kidney, lung, or bone marrow transplant, then built a matched comparison group of sclerosis patients without transplantation, matched two-to-one on age, sex, and race before chart review narrowed things down to forty-eight transplant patients and forty-five non-transplant patients with usable data. This matched-cohort design is a sensible choice here — you can't randomize transplant status, obviously, so matching on the major confounders up front is the practical way to make the two groups comparable before you even look at outcomes. The statistical workhorse is relative risk, essentially just the ratio of cancer incidence in the transplant group over the non-transplant group — a simpler and more interpretable measure than something like a hazard ratio when you're not dealing with heavy censoring or variable follow-up time, which fits a cohort this small. The results: transplantation was associated with roughly a five-fold increase in overall skin cancer risk and about a four-and-a-half-fold increase in keratinocyte carcinoma specifically, both statistically significant. Transplant patients also averaged more than two skin cancers each, compared to about one in the non-transplant group. When they restricted the analysis to cancers arising only after transplantation, the elevated risk persisted, driven mainly by squamous cell carcinoma. The sex-stratified analysis is the most interesting wrinkle — the increased risk was significant in women, with roughly a three-and-a-half-fold increase in both overall skin cancer and keratinocyte carcinoma, but men showed no significant difference between transplant and non-transplant groups, though the male numbers were quite small. Transplant type — kidney, lung, or bone marrow — didn't show a significant association on its own. The authors frame this as suggesting that transplantation, not sclerosis itself, may be the real driver of elevated skin cancer risk in this population, and they speculate the sharper effect in women might reflect a bigger relative loss of immune surveillance that is normally more robust in women than in men — though they're appropriately careful to flag that as speculative. The honest limitations are real: this is a single-health-system retrospective cohort with a small final sample, especially once split by sex or transplant type, so those subgroup confidence intervals are wide and some male-specific comparisons didn't reach significance partly from being underpowered rather than truly null. They also couldn't adjust for immunosuppressive regimen intensity in any robust statistical sense, though descriptively, drug regimens looked similar between transplant patients who did and didn't develop skin cancer. Practical takeaway: this isn't practice-changing in the sense of a new guideline, but it is a useful awareness signal. If you're managing a patient with systemic sclerosis who has had an organ transplant, especially a woman, you should have a lower threshold for close skin cancer surveillance — this cohort supports what many of us probably already intuit from managing transplant patients generally, but it's reassuring to see it specifically quantified in the sclerosis population, and it supports the authors' call for dedicated surveillance protocols in this overlap group. Third is a letter to the editor commenting on the recently published Delphi consensus guidelines on topical combined five-fluorouracil and calcipotriene — the five-FU slash C regimen — for actinic keratosis and superficial keratinocyte carcinoma from the International Transplant Skin Cancer Collaborative. This is a critique piece, not original data, and it raises three methodological concerns worth knowing if you're going to start using or recommending this regimen. First, the original guidelines anchor their efficacy claim on an eighty-seven percent reduction in lesion count, but the letter writers point out that complete clearance — the metric that actually predicts long-term chemoprevention — was much lower in other published data, around twenty-seven percent on the face at eight weeks in a separate systematic review. That's a meaningful distinction: a big drop in lesion count sounds impressive, but if only about one in four patients achieves complete clearance, the guidelines may be overstating real-world curative potential by leaning on the more favorable metric. Second, the guidelines endorse this topical regimen for squamous cell carcinoma in situ without being explicit about whether pretreatment biopsy confirmation is required. The letter cites upstaging data — when biopsy is compared against definitive surgical specimens, discordance rates run surprisingly high, with punch biopsies under-calling invasive disease around twenty-eight percent of the time and shave biopsies around eighteen percent. Even in the best-case scenario, a large cohort of routine superficial biopsies still had about one in five hundred cases upstaged to invasive disease — and for that one patient, treating with topical therapy instead of surgery could mean a meaningfully delayed diagnosis. Third, the guidelines use clinical complete response as the efficacy endpoint, but the letter cites pilot data showing that even when lesions look clinically clear, somewhere between twelve and seventeen percent still harbor residual disease histologically after treatment. Clinical eyeballing, in other words, isn't a reliable substitute for tissue confirmation. The letter closes with three concrete asks for future guideline revisions — anchor treatment duration decisions on complete clearance rather than lesion-count reduction, recommend pretreatment biopsy for higher-risk lesions such as those over a centimeter or in H-zone locations, and consider post-treatment histologic or confocal confirmation in future trials, with a practical nod toward reserving that confirmation step for larger or recurrent lesions given real-world access constraints. There's no new data here, so nothing is practice-changing on its own, but if you're counseling patients about this regimen, it's a useful reminder to be precise about what "it worked" actually means, and to keep your threshold for biopsy low before committing a suspected superficial squamous cell carcinoma in situ to topical-only management. Last up, a brief report using the TriNetX real-world federated database to look at nonmelanoma skin cancer development after immune checkpoint inhibitor therapy. The clinical question is whether checkpoint inhibitors, which unleash immune surveillance, actually protect against subsequent keratinocyte carcinoma — there's been chatter about a possible chemopreventive effect — or whether, conversely, they might unmask subclinical tumors and increase risk. Prior data has been mixed and come from small, heterogeneous cohorts. Methodologically, this is where it gets statistically interesting. The authors pulled adults with melanoma, lung, bladder, or kidney cancer who were treated with or without a checkpoint inhibitor, excluded patients on cemiplimab or who died within the outcome window to reduce confounding and misclassification, and then used propensity score matching, stratified separately for patients with and without a prior nonmelanoma skin cancer history. Propensity score matching is the right tool here because you can't randomize who gets a checkpoint inhibitor — patients who receive these drugs differ systematically from those who don't, in disease stage, comorbidity, oncologic urgency, and so on. The technique works by building a statistical model that estimates each patient's probability of receiving the checkpoint inhibitor based on their measured characteristics, then pairing treated and untreated patients with similar probabilities, so that on average the matched groups look comparable across all those measured confounders — essentially trying to recreate, after the fact, something closer to a randomized comparison using observational data. Outcomes were then compared using Cox hazard ratios, which measure the relative instantaneous risk of developing cancer at any given moment during follow-up, appropriately handling the fact that patients had varying lengths of observation. And because the authors tested multiple skin cancer subtypes and several outcome windows, they applied the Benjamini-Hochberg correction, a method for controlling the false discovery rate when you're running many simultaneous statistical tests — it adjusts your significance threshold so you're not fooled by chance findings that pop up simply because you looked at enough different outcomes. They also built in negative controls, seborrheic keratosis and benign cutaneous destruction procedures, biologically implausible targets for a checkpoint-inhibitor effect, as a sanity check against residual confounding or detection bias — a smart design touch that's worth noting as good methodological practice generally. The results, in patients without a prior nonmelanoma skin cancer history, over twenty-one thousand per matched cohort: overall nonmelanoma skin cancer risk was not significantly different with checkpoint inhibitor exposure. But when split by subtype, cutaneous squamous cell carcinoma risk was significantly higher, about a thirty percent relative increase, while basal cell carcinoma risk was significantly lower, down by about seventeen percent. Total procedure burden didn't differ between groups. In patients with a prior nonmelanoma skin cancer history, a smaller matched cohort of around twenty-three hundred per group, basal cell carcinoma risk was again significantly lower with checkpoint inhibitor exposure, and total procedure burden was modestly but significantly lower too, while squamous cell carcinoma and overall nonmelanoma skin cancer showed no significant difference. The negative controls stayed quiet throughout, which supports the internal validity of the matching. The authors' interpretation is a clean subtype-specific story — checkpoint inhibitors may be unmasking subclinical squamous cell carcinomas through immune-mediated inflammation, consistent with prior case reports of eruptive squamous cell carcinomas after programmed death-1 blockade, while appearing to enhance immune clearance of the less immunogenic basal cell carcinomas. But they're explicit, and I think appropriately so, that these are statistically significant yet clinically modest effect sizes — hazard ratios hovering in the range of zero-point-eight to one-point-three are not the kind of signal that should change how you counsel a patient starting immunotherapy. Limitations include residual confounding inherent to any observational database study, reliance on diagnosis codes rather than chart-confirmed pathology, and the exclusion of cemiplimab, which limits generalizability given how commonly that agent is now used specifically for skin cancer indications. Practical takeaway: this is genuinely interesting but not practice-changing. It doesn't support using checkpoint inhibitors as a chemopreventive strategy, and it doesn't warrant dropping your skin cancer screening to the general population baseline for patients on these drugs. What it does reinforce is clinical common sense that's already out there anecdotally — keep an eye out for new or rapidly growing squamous lesions in patients on checkpoint inhibitors, since there may be a real, if modest, biological signal toward unmasking squamous cell carcinoma specifically, even as overall keratinocyte carcinoma burden doesn't change much. That wraps our four pieces for this issue — a call for transparency as AI enters our review literature, a reminder that transplantation likely drives excess skin cancer risk in systemic sclerosis patients, a sharp methodological critique of the new five-FU-calcipotriene consensus guidelines, and a nuanced, subtype-specific look at checkpoint inhibitors and keratinocyte carcinoma risk. Thanks for listening, and I'll see you next issue.