For a condition that affects millions of people, long COVID has produced remarkably few clear answers. Patients who have been sick for years hear the same things they heard in 2021: we are studying it, we do not yet know the mechanism, there is no approved treatment.
It is tempting to read that as failure. It is more accurate to read it as the slow, frustrating phase of science where hypotheses are being ruled out. The field’s most important recent results have been negative ones. That is progress, but only if we learn the right lesson from it.
First, agreeing on what we are studying
For years, long COVID research suffered from a basic problem: studies defined the condition differently, so their results could not be compared. In June 2024, the US National Academies of Sciences, Engineering, and Medicine published a definition. It describes long COVID as an infection-associated chronic condition that occurs after SARS-CoV-2 infection, is present for at least three months, and can be continuous, relapsing and remitting, or progressive, affecting one or more organ systems.
The definition is deliberately broad. It covers fatigue and post-exertional malaise, but also diagnosable conditions such as postural orthostatic tachycardia syndrome, myalgic encephalomyelitis/chronic fatigue syndrome, arrhythmias, interstitial lung disease, diabetes and autoimmune disorders.
That breadth is honest about how varied patients’ experiences are. It also exposes the central research challenge. Long COVID is very likely not one disease with one mechanism, but several overlapping ones sharing a trigger.
How many people?
Estimates vary with method, but they are large. The US Centers for Disease Control and Prevention’s Household Pulse Survey found that in March 2024, about 7 per cent of all US adults, roughly 17 million people, reported currently having long COVID. Self-reported surveys have limits, but even conservative readings put the numbers in the millions in the US alone, with a real effect on employment and disability.
The antiviral test
One leading hypothesis is that fragments of the virus, or the virus itself, persist in the body and drive ongoing symptoms. If so, an antiviral might help. This was a reasonable, testable idea, and it has now been tested.
In June 2024, the STOP-PASC trial from Stanford, published in JAMA Internal Medicine, found that a 15-day course of nirmatrelvir-ritonavir (Paxlovid) was safe but did not significantly improve selected long COVID symptoms compared with placebo. A separate decentralised trial, PAX LC, published in The Lancet Infectious Diseases in 2025, enrolled 100 participants from their homes across the US and also found no benefit over placebo at 28 days.
Look at the size of those trials. They are phase 2 studies, built to spot a large effect across a broad population, not to rule out a modest effect in a subgroup. That is both their value and their limit. They can tell us a broad effect is unlikely; they cannot tell us nobody benefits.
For patients hoping for a quick fix, these results were a disappointment. For the field, they were useful. Viral persistence may still matter for some patients, but a short antiviral course is not the general answer.
Why negative results are worth more than they look
A negative trial is only informative if it was designed well enough to have found something. Both antiviral studies were randomised and placebo-controlled, which is why their null results carry weight. Compare that with the alternative that filled the vacuum in the early pandemic years: observational reports, patient testimonials and off-label prescribing, which produce plenty of hope and very little knowledge. A well-run negative trial closes a door honestly. It saves future patients from spending money and months on a treatment that probably will not help them, and it frees research money for the next hypothesis.
There is a cost, and patients bear it. Each null result lands on people who have been ill for years and read the headline as “nothing works”. That is not what the trials showed. They showed that one specific regimen, given to a broadly defined group for a fixed period, did not produce an average benefit on the outcomes measured. The distinction sounds pedantic. For someone deciding whether to keep hoping, it is not.
The uncomfortable lesson: we need subtypes, not bigger trials
Here is where the conventional take goes wrong. When a trial in a heterogeneous condition fails, the usual response is to run a bigger trial. But if long COVID includes several different mechanisms, a treatment that works well for one subgroup can look useless when averaged across everyone.
That means the most important research investment may not be more drug trials. It may be the unglamorous work of dividing patients into biologically meaningful groups first: people with evidence of persistent virus, people with autonomic dysfunction, people with immune dysregulation, people whose illness resembles ME/CFS. Trials that enrol by subtype are more likely to find signals that broad trials miss.
The arithmetic of dilution
A simple calculation shows why. Imagine, for illustration only, that a drug works well in patients whose illness is driven by persistent virus, improving a symptom score meaningfully in half of them, and does nothing for everyone else. Now suppose that group makes up a fifth of a broadly recruited trial. The true responders are then one in ten participants. A trial of 100 people, split between drug and placebo, would contain around five responders on the active arm, sitting inside the ordinary noise of placebo response and day-to-day fluctuation in a relapsing condition. The drug “fails”. Nothing about the drug has been learned.
Double the trial size and the problem does not go away. The effect is still diluted by the same factor; you just need a much larger sample to detect it, and a large, expensive trial that finds a small average benefit invites the next objection, that the benefit is clinically trivial. Enrich the trial with the right patients and the same drug could show a clear signal in far fewer people. The numbers here are invented to show the shape of the problem, not to describe any real drug. The shape is what matters.
The strongest counterargument
The case against phenotype-first research is not foolish. Biomarkers for long COVID subtypes are still immature. Nobody yet has a validated blood test that says “this patient has viral persistence” with enough reliability to base enrolment on it. Waiting for perfect subtyping before running trials could mean waiting years while patients stay sick, and some treatments may work across subtypes after all. Broad pragmatic trials also have an advantage: their results apply to the patients doctors actually see.
This partly holds. The answer is not to stop trials until phenotyping is finished but to build it into them: collect biological samples and detailed symptom profiles in every trial, pre-specify subgroup analyses with a biological rationale, and design adaptive trials that can enrich for responders as signals appear. That turns each negative trial into a data source for the next one instead of a closed door. The failure mode to avoid is the one where a trial reports only its primary endpoint, deposits nothing reusable, and leaves the field no wiser about who might have benefited.
There is an incentive problem here. Funders and journals reward trials with clear endpoints and fast results. Careful phenotyping takes years and produces descriptive papers that attract less attention. Yet without it, the field risks testing good ideas in the wrong patients and declaring them failures.
There is also a historical warning. Patients with ME/CFS, which the National Academies definition explicitly lists among long COVID presentations, spent decades being told their illness was poorly understood and, too often, that it was not entirely real. Research money stayed thin because the condition was hard to define, and it stayed hard to define because research money was thin. Long COVID has, for now, much more attention and funding. The risk is that a run of negative trials makes funders conclude the problem is intractable and move on, repeating the same cycle with a far larger patient population.
What funders and ministries should change
Research funders hold the biggest lever. They can pay for shared infrastructure, such as biobanks, harmonised symptom measures and common data standards, so that dozens of small trials add up to something rather than sitting in separate silos. They can also judge applications partly on whether a trial will leave reusable data behind. A negative result with good samples attached is worth far more than a negative result alone.
Health ministries and payers face a different question: what to fund while evidence is thin. The temptation is to wait for a drug. The better investment is in clinics that can recognise the treatable components of long COVID, and in employment and disability arrangements that stop a chronic illness from becoming a permanent exit from work. Those costs land on labour and social protection budgets as well as health ones, which is another reason the condition tends to fall between ministries.
For founders and drug developers, the lesson is commercial as much as scientific. A company testing a drug in an unselected long COVID population is buying a lottery ticket with poor odds. One that invests in a biomarker to find its likely responders has a better chance of a clean result and a clearer label.
What clinicians can do while the science catches up
The absence of a specific drug is not the absence of care. For patients whose symptoms worsen after exertion, pushing harder can make things worse, so post-exertional malaise needs to be taken seriously: pacing is a treatment, not a surrender. Much of what patients have can be diagnosed and treated on its own terms. POTS, sleep disorders, new diabetes and cardiac problems have established treatments whether or not they arose from COVID.
Clinicians can also support work, not just bodies. Graduated returns, adjusted hours and disability documentation keep people from falling out of the workforce entirely. And they can enrol patients in well-designed studies, because every clearly defined participant makes the next trial smarter.
What to watch
Over the next 12 to 24 months, the useful signals are specific. Watch whether new trials enrol by biological subtype or symptom cluster rather than by the broad definition alone. Watch whether larger, better-powered antiviral studies report subgroup data rather than a single average. Watch funding decisions: whether long COVID research budgets hold up after a string of negative results, or start drifting away as ME/CFS budgets did. And watch whether clinical services survive the end of pandemic-era emergency money, because patients will need them long after the headlines move on.
The takeaway
Long COVID research has not failed. It has done the hard work of eliminating simple answers, which is how complex conditions usually yield. The next phase will depend less on the next big trial than on whether researchers and funders are willing to invest in understanding who, exactly, they are treating. A field that learns to read its failures as maps rather than verdicts will get to treatments faster. A field that reads them as proof of futility will lose its funding, its best researchers and the trust of patients who have already waited long enough.
For clinicians and patients: which long COVID subtypes do you think research is overlooking? Share your view in the comments.
