Not All Data Is Created Equal: How to Read the Evidence Behind a Wound Care Claim
By Nikolai Sopko, MD, PhD
President, Chief Scientific Officer & Chief Operating Officer, PolarityBio
Walk any wound care exhibit hall and you will hear words like "clinically proven," "shown to heal," or "regenerative." The words sound impressive. The evidence behind them is not always equally strong. One product may rest on a large, randomized trial. Another may rest on a handful of treated cases written up by the company that sells it. Both can end up on a slide with the phrase "clinically proven" underneath.
For clinicians and health systems deciding what to put on a patient's wound, the claim itself is the wrong place to stop. The better question is not whether a product has data. The better question is how much weight that data can actually bear.
Having spent my career at the intersection of medicine, science, and product development, I have read a great many of these studies from both sides — as a clinician deciding what to use and as someone responsible for generating the evidence. This piece is a short field guide to reading them. It walks through what separates rigorous evidence from fragile evidence and where common study types in wound care sit on that scale.
Evidence Sits on a Hierarchy
Medicine has spent decades formalizing the idea that some study designs support stronger conclusions than others. Chronic wounds are noisy. Patients differ in perfusion, glycemic control, offloading, adherence, and infection. A good study design earns trust by controlling that noise so that improvement can be credited to the therapy rather than to chance, patient selection, or the natural history of the wound.
From weakest to strongest, the usual ranking runs roughly like this:
Mechanistic reasoning and expert opinion: A plausible biological story about why something should work. Useful for generating hypotheses, insufficient for proving benefit.
Case reports and case series: One patient, or a collected group of patients, treated and described. No comparison group. Easy to see who did well, but unclear who would have done well anyway.
Retrospective observational studies: Chart reviews and registry pulls assembled after the fact. Larger numbers and real-world breadth, but the patients were never randomly assigned, so the sickest and the healthiest sort themselves into groups in ways that bias the result. Valuable for describing practice patterns and generating hypotheses; weak ground for establishing that a therapy works.
Prospective cohort and case control studies: Planned in advance, which helps, but still without randomization.
Randomized controlled trials: Patients assigned by chance to the therapy or to a control, which balances both the factors you can measure and the ones you cannot.
Systematic reviews and meta-analyses of randomized trials: A disciplined synthesis of the strongest studies, when those studies exist and are well conducted.
However, a sloppy or rushed “randomized” trial can be worse than a careful cohort study. What matters is the specific features of rigor underneath.
The Features That Actually Separate Strong Data from Weak Data
Rather than memorize the hierarchy, look for these design choices:
A comparison group: Without a control arm, an impressive healing rate means very little, because a meaningful share of chronic wounds close with attentive, good quality standard care alone [1]. "Eighty percent healed" is only interpretable next to what happened in similar patients who did not receive the therapy. Both ADA compendia caution specifically against lining up healing percentages from separate trials as though they were equivalent, because the studies differ in design, rigor, entry criteria, and follow-up [1,2].
Randomization: Random assignment is the only tool that balances the confounders nobody thought to measure, which is what makes it the foundation of a fair comparison. Studies that let the clinician or the patient choose the treatment almost always flatter the newer product.
Blinding of outcome assessment: Wound closure is a judgment call at the margins. When the person measuring the wound knows which treatment it received, that knowledge leaks into the measurement. Blinding is also harder to achieve in wound care than in a typical drug trial. Topical products often have a distinct appearance, a placebo or sham dressing can itself impair healing, and for an autologous therapy a sham procedure may not be ethical. Independent, masked assessment protects against it.
A prospective, prespecified plan: Strong studies declare their primary endpoint and their analysis before the first patient enrolls, often by registering the protocol publicly. Weak studies decide what counts as success after the results are in, which is how a therapy that missed its main goal still produces a press release.
An intention-to-treat analysis: Rigorous trials analyze every patient in the group they were assigned to, including the ones who dropped out or did poorly. Analyses that quietly exclude non-completers, sometimes labeled per protocol, tend to inflate the apparent benefit. The ADA compendium documents a wound therapy whose reported benefit rested on a per-protocol analysis of roughly 35 patients rather than an intention-to-treat analysis [1].
Adequate size and honest statistics: Small studies swing wildly and tend to overstate effects. A study that reports one impressive finding out of twenty comparisons has usually found noise, not signal. The same caution applies to subgroup claims, where a benefit in "patients like these" often evaporates on repeat testing. The ADA compendium describes a product reporting 95 percent healing versus 35 percent in controls at six weeks — in a trial of 40 patients, only 20 of whom received the product — and notes that later effectiveness data did not reproduce such dramatic results [1].
A population that resembles real patients: Data drawn from a narrow or unrepresentative group does not transfer to the clinic. This cuts both ways. Some studies enroll only the healthiest wounds and then market to the hardest. Others assemble convenience samples that no one designed to answer the question at all.
Independent funding and peer review: Industry funding does not automatically invalidate a study, and much good research is sponsor supported. But a trial funded, run, analyzed, and reported by the company that profits from the result, then published outside peer review or only as a conference poster, has cleared very few checks.
Some Familiar Examples of Thin Evidence
None of the following is fraudulent, and none is bad science on its own terms. Each has a legitimate use. The problem in every case is the same: a study design being asked to carry a claim it was never built to support.
The single-arm case series: A company reports that a large percentage of treated wounds healed. There is no control group, no randomization, and often no independent assessment. Case series are useful for describing technique, safety signals, and unusual presentations. What they cannot do is separate the therapy from the healing that good ordinary care would have produced anyway — so an impressive percentage, standing alone, proves almost nothing about benefit.
The retrospective registry analysis offered as proof of efficacy: Real-world data earns its place. For a therapy already proven in trials, careful cohort-matched registry work shows how it performs in ordinary practice, across wound types a protocol excluded, over longer follow-up. The misuse is presenting it as the primary evidence that a therapy works. Propensity methods adjust only for differences someone thought to record, never for the ones nobody measured, and sample size does not repair that.
The post hoc subgroup used to rescue a failed endpoint: Exploratory analysis is normal and valuable. A trial that meets its primary endpoint and then asks which patients benefited most is doing exactly what it should. The problem is narrower: a study misses its endpoint, and a subgroup defined after the results were known becomes the headline. Slice a dataset enough ways and something will look impressive by chance. That is a hypothesis worth testing, not a demonstrated benefit.
The regulatory label used as a clinical claim: "FDA registered," "FDA cleared," and "FDA approved" are not interchangeable. They describe three different levels of review, and only some of them require evidence that the product heals wounds at all. A product can be legitimately registered with the FDA and never have been tested for effectiveness. This is the most common source of confusion in wound care, and we will take it up in our next Polarity Perspective.
A Short Checklist for Any Study
The next time a study is put in front of you, these questions cut through most of the noise:
Was there a comparison group, and were patients randomly assigned to it?
Was the primary endpoint defined before the study began?
Were the people measuring the outcome blinded to the treatment?
Were all enrolled patients analyzed, or were non-completers dropped?
How many patients were studied, and was the study large enough to support the claim?
Did the population resemble the patients you actually treat?
Was the study registered in advance?
Who funded, ran, and analyzed it?
Where was it published and was it peer reviewed?
A therapy worth using should welcome these questions. I would rather field them about our own work than have a clinician adopt something on the strength of a slide. The strongest evidence in wound care has nothing to hide, and the difference between data that can carry weight and data that cannot is usually visible within a minute of asking.
This article is educational and reflects general principles of evidence appraisal in wound care. It does not describe or make claims about any specific product. I would encourage anyone weighing a therapy to follow the references and read the underlying studies directly. PolarityBio's SkinTE® is available for investigational use only.
References
1. Boulton AJM, Armstrong DG, Kirsner RS, et al. Diagnosis and Management of Diabetic Foot Complications. Arlington, Va.: American Diabetes Association, 2018. doi:10.2337/db20182-1.
2. Boulton AJM, Armstrong DG, Löndahl M, et al. New Evidence-Based Therapies for Complex Diabetic Foot Wounds. Arlington, VA: American Diabetes Association, 2022. doi:10.2337/db2022-02.
