Zapping back muscles back to life: restorative neurostimulation
Hardly a day goes by in my job without someone showing me a study with positive results that are hard to believe. Almost none of them are credible, because there is so much terrible research out there. But it’s easy to underestimate just how much, and how bad. To demonstrate just how unbelievable most of these positive results really are, today I’m going to really tear apart a new study that says a spinal muscle stimulator is effective — a particularly good example of a bad clinical trial.
And what a marvellous opportunity it would be if, for once, we could compare this bad study to a much higher-quality study of exactly the same thing with a negative result? That would be an excellent reason to choose this bad example! Yes indeed, that would sure be nice.
The citation and a disclaimer
Here’s the low-quality “positive” trial I’ll be zooming in on:
Schwab F, Mekhail N, Patel KV, et al. Restorative Neurostimulation Therapy Compared to Optimal Medical Management: A Randomized Evaluation (RESTORE) for the Treatment of Chronic Mechanical Low Back Pain due to Multifidus Dysfunction. Pain Ther. 2025 Feb;14(1):401–423. PubMed 39812968 ❐ PainSci Bibliography 49289 ❐
The authors call it the “RESTORE” trial, but it’s not “the” RESTORE trial, so I will not be calling it that.
⚠️ This article expresses my opinion based solely on publicly available scientific papers. It is not intended to impugn the integrity of any researcher or company. This is an abstract critical analysis of the concepts and science, not a product review, which is why I have not named any specific manufacturer or product here.
The treatment idea: an implanted spinal muscle stimulator
This is about another kind of zapping treatment, right on the heels of last week's extremely skeptical summary of microcurrent therapy. This one is about stimulating deep spinal muscles with electricity to save people from back pain that is supposedly caused by those muscles being asleep on the job — so why not shock them back to life?! They call this a “restorative neurostimulation” device, and it is surgically implanted: there’s an electrical generator about the size of an AirPods case tucked into a subcutaneous “pocket,” and a pair of wires that snake their way into the anatomy of the spine (see figure 1 in a related study).
This was done for an allegedly specific kind of chronic low back pain patient — the ones with presumed muscle dysfunction (multifidus, one of several deep spinal muscle groups). The rationale and theoretical mechanism here is that repetitively stimulating muscle activation can “override neural inhibition” and revive multifidus function to restore spinal stability.
Maybe it can and maybe it does … but all of that “why” stuff is speculative and implausible. (Note that there are other kinds of spinal/deep electrical stimulation that may be more effective at treating chronic pain; I’m only digging into this one specific idea today.)
The test basics
The researchers found 203 adults with long-standing mechanical low back pain and vague signs of multifidus dysfunction, and assigned half of them to get treatment with the gadget (plus ongoing usual care). The other half got only “optimal” medical management. The primary outcome at 1 year was disability (Oswestry Disability Index, ODI). Pain was a secondary outcome, along with quality of life.
Their results favored the device by quite a bit, ODI improvements of ~20 versus just ~3 with OMM; pain fell three points more than the control group; and quality of life rose only slightly, but again quite a bit more than the control group.
There were some problems with the implants: 23% of patients had adverse events at 1 year, which is about what you’d expect from an implant. None of these side effects were all that serious — mostly overstimulation, “pocket pain” and irritation, a couple infections — but also nothing you want to put up with for the sake of an unclear benefit.
The flaws: why those “big” effects are almost certainly an illusion
I see at least nine major “validity threats” in this paper, nine reasons that the results probably don’t mean what we are asked to believe they mean.
We’re taking this post to dork factor nine now — if you’re not interested in the details, skip to the bottom line. But the details are the point of this post. If you subscribed because you want to learn how to think about the science of pain, this is what you signed up for. 🙂
1) Open-label design + subjective outcomes = maximum bias risk!
No blinding is a huge weakness, but it really starts to stink in combination with patient-reported outcomes. Expectation and performance bias can powerfully inflate apparent benefits when there’s surgery and a visible, “active” treatment. The authors argue a 1-year endpoint outlasts placebo/nocebo, but open-label surgical/device trials routinely overestimate effects compared to sham-controlled designs.
2) The control condition looks constrained and unusually “flat,” but unequal attention and co-interventions favor the device arm!
The “optimal medical management” for the control group was pre-specified, with providers instructed to minimize medication changes after “optimization” to avoid confounding … which could certainly suppress improvements in the control arm that you'd normally expect. Meanwhile…
Device patients had multiple follow-ups with parameter adjustments, extra clinical TLC, which is a recipe for classic performance bias. More touchpoints, coaching, and perceived care can easily improve patient-reported outcome measures regardless of the specific mechanism (“time + attention” effect).
3) Size of the between-group effect is implausibly large for this population.
They powered this study based on an expectation of a 12-point ODI improvement in OMM, but observed only ~3 points — a weirdly poor control outcome that magnifies the relative superiority of the zappy gadget. In real-world chronic LBP, standard care often yields modest but non-trivial gains. But here? It barely budged at all. It’s quite fishy.
4) Modified intention-to-treat and missing-data handling choices can shape the result.
In clinical trials, some people don’t finish — they drop out, miss visits, have surgery, move away, get side effects, or just ghost the researchers. How you deal with that missing data can make your results look better or worse. These researchers didn’t count everyone, and they made some “optimistic” guesses about people who dropped out. Their methods were defensible enough on paper, but they are a validity threat in the context of some of these other flaws. For instance, they excluded anyone without a single post-baseline measure — which can bias results toward benefit.
The bottom line is that this is another mechanism for inflating the results — another way a weak signal can look stronger.
5) Diagnosis of “multifidus dysfunction” mixes subjective tests with uncertain external validity.
Every note of the rationale for this treatment is speculative, just a weak conceptual foundation:
- The study does not show that multifidus is inhibited in the first place. The authors didn’t even select their patients with a credible diagnosis of multifidus dysfunction: they used unreliable physical tests, non-specific imaging signs of dubious relevance, and all without any comparison to a baseline. There are no pre-implant or post-implant measures of multifidus size, activation, or recovery in this paper.
- It’s also not clear that multifidus dysfunction, even if it exists, leads to “instability,” and of course instability isn’t measured either — it’s just a hypothetical. Nor is it clear that subtle instability is actually a mechanism for low back pain; that has always been a poorly supported story about what drives back pain.
- And finally it’s not demonstrated that the device can actually improve multifidus function, let alone that it can specifically “override inhibition.”
It’s not inherently wrong to speculate about the causes of back pain and how it might be treated … but it quickly becomes a problem when you start trying to choose people to be in your clinical trial when you can’t actually know whether or not they have a specific problem. The whole point of careful subject selection in trials is to eliminate a good half dozen notorious sources of “selection bias.” The validity of the test suffers in proportion to the vagueness of the inclusion criteria. In this case, for instance, there’s a significant risk of choosing study subjects that aren’t really what you think they are, and may be primed to respond to any intervention framed as “restorative.”
6) Industry funding and extensive conflicts increase spin/confirmation risk.
This trial was funded by the maker of the device being tested. And many investigators had relationships with device companies. The conflict of interest declarations run for more than a full page. As I have often acknowledged, bias isn't a deal-killer in itself — but it is a red flag, and it gets much larger and starts flashing when combined with all these other flaws.
7) Safety profile is non-trivial for a therapy pitched as “restorative.”
This is an “invasive” therapy, and it shows: almost a quarter of the subjects had device/procedure/therapy-related adverse events. The leads broke and came out. Patients might accept these risks if the benefit was real and durable, but these harms matter against a background of extremely uncertain efficacy.
8) Generalizability is so narrow that even a believable positive result would have limited value.
The study excluded patients who'd gotten prior lumbar surgery, had a BMI over 35, active smokers, radicular pain worse than back pain, and quite a bit more — more than is typical for back pain trials. These factors are common in real-world back pain, so they were testing a treatment only for one very specific kind of patient.
Narrow inclusion criteria aren’t always bad. They’re useful in studies of how or why something might work: eliminating noise helps isolate physiological effects. But for effectiveness testing, those same exclusions create an artificial, idealized patient group that doesn’t reflect the messy diversity of real-world cases. Even if the treatment seems to work in that small, hand-picked population, the narrow selection criteria boost the risk that a happy result is only positive “in the lab,” not in real patients that are older, heavier, and more medically complicated.
9) No objective functional endpoints.
There were no objective measures of strength, endurance, or activity (e.g., accelerometry), nor return-to-work data. All primary inferences rest on self-report scales in an unblinded setting.
A pitch-perfect example of low quality science
Schwab et al. has a fatal combination of many serious flaws: a dubious rationale, open-label surgical/device intervention, subjective outcomes only, a constrained and unusually stagnant control, heavy industry involvement, low generalizability, “optimistic” handling of drop-outs, and non-trivial harms. All that does not just “cast doubt” on the large reported effects — it makes them impossible to trust at all. These aren’t “promising” results, they’re just meaningless.
I would bet almost anything that a properly sham-controlled trial would produce obviously inferior results. But I don’t have to bet, because that already happened. How convenient! I didn’t know this when I started writing this post. I cackled when I found it.
Gilligan et al tested exactly the same treatment, and it shares many of the same flaws, including the off-the-charts risk of bias. Despite that, it is a much more credible study, thanks to much better design — double-blind and sham-controlled! Controlling the effect of bias is the whole point of science. And it had an officially negative result: superiority of the device was not shown within the planned timeframe. They tried to tame the bad news by focusing on some minor positive results longer-term, leaning heavily on the words “trending positive” … but that just damns the results with faint praise.
- The bad study is positive but unbelievable.
- The much more believable study is negative.
More study probably not really needed.