Pimobendan in preclinical stage B2 mitral valve disease: where the effect comes

1What the trial reported

EPIC randomised dogs with preclinical myxomatous mitral valve disease and cardiomegaly to pimobendan or placebo, and reported a median time to the primary endpoint of 1228 days against 766, a hazard ratio of 0.64 and a log-rank P of .0038.¹ The primary endpoint was a composite: the onset of congestive heart failure, cardiac death, or euthanasia for cardiac disease.

It is the best-conducted trial in canine cardiology, and it is the basis on which pimobendan is now licensed for stage B2 disease. This appraisal takes the result seriously enough to ask how much of it survives close examination, and it then sets that examination beside what the regulatory record actually says.

2Rebuilding the trial

The published survival curves were digitised and approximate individual-level event times reconstructed from them, so that analyses the paper does not report could be run. These are pseudo-individual event times recovered from the curve rather than the trial’s own patient records, and nothing here recovers an actual dog. Group sizes and total event counts were fixed to the published values, whereas medians, hazard ratio and P were left free, so that agreement with the paper serves as a genuine check rather than as an assumption.

The same procedure on the all-cause mortality curve gives medians of 1058 and 901 days against a published 1059 and 902, and a hazard ratio of 0.652, which the paper does not report.

Read this section with the reconstruction in mind. Everything that follows in sections 3 to 7, and the modelling in section 14, is computed on reconstructed data, not on the trial’s own dataset. Reconstruction from published curves recovers group-level quantities well and individual dogs only approximately. The agreement shown above is a reason to take these analyses seriously, and it is not a substitute for the investigators running them on the original data.

3When the separation happens

By day 180 the placebo arm has accrued 27 events against 11 on pimobendan. The gap of 16 events at that point is already larger than the 14-event difference with which the trial finishes. Over the whole of the remaining follow-up the two arms accrue 63 and 61 events respectively.

The entire absolute separation between the arms therefore occurs within the first six months, and after that point the two curves fall at the same rate.

4Dropping the early period

If the effect were confined to that early period, removing it should dissolve the result. Removing the first several weeks from both arms and restarting the clock:

Significance goes at 23 weeks, with 134 of the original 162 events still in hand.

Taken on its own that is only a power argument, and it deserves to be dismissed as one, because a quarter of the events have gone and the point estimate has moved no further than from 0.63 to 0.71. The argument works only as a comparison. The last column is the P that would be expected if the hazard ratio never changed and the only thing lost were events, taken from the standard approximation SE(log HR) = 2/√d. At 134 events a constant effect of 0.630 would still give P = 0.0075. What is observed is P = 0.0501, nearly seven times higher.

The observed P deteriorates faster than the loss of events can account for. The divergence between the observed and expected columns is therefore the argument, and the bare loss of significance is not.

5What survives the cut

Losing significance is not the same as losing the effect. Restarting the clock at 23 weeks and asking what is left:

Restricted mean survival is calculated to 1200 days and does not depend on where the curves cross fifty per cent. In calendar terms the day-161 analysis puts the medians at 1225 and 845 days from randomisation.

Conditioning on a dog being alive and event-free at six months, the median gap is therefore still 380 days and the average event-free time gained is still 107 days. Those figures are smaller than the headline result and they are a long way from nothing. If the whole result were composed of early failures, the residual gap among dogs nowhere near heart failure at six months should be small, and it is not.

6How fragile the result is

Placebo events were taken latest-first and reclassified as censored, which is the least favourable realistic change that could be made to the data. This is a sensitivity analysis rather than the conventional fragility index, because the fragility index converts events to non-events in the smaller arm of a two-by-two table, whereas the procedure used here reclassifies late events as censorings in a time-to-event analysis. The counts below are therefore not comparable to published fragility indices and are not offered as such.

Nine dogs are sufficient. Reclassifying nine late placebo events as censored causes the trial to lose significance. For scale, the journal and FDA accounts of this same trial differ from each other by more than that, since the control arm gains three events between the two documents and loses six dogs.

7Timing, not counts

Judged on proportions alone, which are 74 of 178 against 88 of 176, Fisher’s exact test gives P = 0.135, which is not significant.

All of EPIC’s statistical significance therefore comes from when dogs had events rather than from how many of them did. Much the same number of dogs reached heart failure in each arm, and they reached it at different times.

This is not in itself a criticism of the trial. Delaying the onset of heart failure is precisely what the drug claims to do, and a time-to-event analysis is the correct way to test that claim. It does, however, explain why the result is so sensitive to any analysis that touches timing, and why nine reclassifications are enough to undo it.

8Three versions on the public record

The 2022 conditional approval and the 2025 full approval both summarise this trial. Neither of them agrees with the published paper, and they do not agree with each other either.

The 2025 summary prints three population figures and they should not be conflated: 363 dogs enrolled, an effectiveness population of 353, and 343 “included in the effectiveness population in the final analysis” (173 pimobendan and 170 control), which is the denominator for the event counts above.⁵

The 2022 version sits almost exactly on the paper, down to the component event counts, whereas the 2025 version has ten fewer dogs and reports a stronger effect. The control arm loses six dogs and gains three events between the two documents, and that is what drags the hazard ratio down.

There is a plausible and innocent explanation, and the documents supply it. The paper describes an endpoint committee reviewing the radiographs and the case records.¹ The 2025 summary states that “each case of CHF was verified by an endpoint committee, under masked conditions, based on the radiographs alone.”⁵ Re-adjudicating the same dogs under a narrower rule would move cases in both directions, which is what the component counts show.

That explanation can be tested directly. On the reconstructed data, removing five and six dogs from the two arms and reclassifying a few early censorings as events reproduces the FDA hazard ratio at 0.596 against their 0.591, the control median at 727 days against 732, and the P at 0.0011 against 0.0008. What the record contains is therefore one dataset under two adjudication rules rather than two different trials.

What is not resolved is that nothing cross-references the three. Anyone citing EPIC is citing one version of it without being told the others exist.

9What the regulator did

The 2025 summary states that EPIC “did not meet certain characteristics of an adequate and well-controlled study [21 CFR 514.117],” and that it was “considered corroborative to support this indication when evaluated in conjunction with Study No. 2019035, a single-arm field study with a historical control.”⁵

The summary never says which characteristics were not met. The regulation is cited, and the deficiencies are not enumerated anywhere in the document.

The 2022 conditional approval was softer, accepting the data as a reasonable expectation of effectiveness.⁴ Pimobendan was therefore marketed for preclinical B2 disease from June 2022 under conditional approval, on a reasonable-expectation standard, for three and a half years before the full approval of 19 December 2025.^{4, 5}

10The pivotal study, and what it was measured against

The study that converted conditional approval into full approval was 2019035: in FDA’s own words a “historically controlled, open-label, multi-center field study,” single-arm, with 125 dogs in the effectiveness population and one year of follow-up.⁵

It reported a treatment success rate of “79.2% (95% confidence interval 70.3 to 85.9%).” The criteria for success were fixed in advance: “the lower bound of the 95% confidence interval was greater than or equal to 54% and the estimated success rate for pimobendan was greater than or equal to 65%.”⁵ Nothing in the document explains where either threshold came from.

The historical comparator was EPIC. The summary states that “the historical control was derived from a subset of the control population enrolled in the EPIC study … that met the enrollment criteria for this study,” and, separately, that applying the new success criteria to EPIC “cases enrolled at US sites … resulted in a success rate of 80% with a lower 80% confidence interval of 72%.”⁵

Two consequences follow from this, and the first of them is the more important.

The success threshold was set below the comparator. If the 80 per cent figure describes untreated EPIC dogs, then the bar the pivotal study had to clear, a point estimate of 65 per cent, sat fifteen points beneath the historical control rate, and the observed 79.2 per cent did not exceed that rate but matched it. The study was never required to beat its own comparator, and the document records no comparison against it. A single-arm design is not worthless in itself. The difficulty is that without a contemporaneous randomised comparator the result depends entirely on whether the historical benchmark describes a population comparable to the one enrolled, and the benchmark used here was set below the rate from which it was drawn.

The derivation of the benchmark is under-specified. The two passages describe the source differently: a subset of the control population meeting this study’s enrolment criteria in one place, and cases enrolled at US sites in another. The two passages are not stated to describe the same dogs. The arithmetic adds to the doubt, because the failure definition in 2019035 is broader than EPIC’s endpoint, so applying it to EPIC must give a lower rate than the event-free rate does. EPIC placebo dogs at LA/Ao 1.8 and above are in the region of 70 per cent event-free at one year on the narrow definition, which does not obviously leave room for 80 per cent on a broader one. That estimate scales the published hazard ratio for LA/Ao by the study’s own failure breakdown. It is arithmetic performed on published numbers rather than a measurement, and it is offered as a reason for stating the derivation rather than as a finding in itself.

Two further features of the design deserve recording. Dogs with “current or previous evidence of clinically significant coughing” or “current or previous evidence of syncope” were excluded; new syncope, and “advanced coughing that required concomitant therapy in absence of radiographic CHF,” then counted as treatment failures.⁵ Entry to the pivotal study also required LA/Ao ≥ 1.8 and VHS > 10.5, with no LVIDDN criterion at all,⁵ so the two studies did not define stage B2 in the same way.

11The label

The approved indication is qualitative: asymptomatic disease with “a moderate or loud mitral murmur due to mitral regurgitation and cardiomegaly.”⁷ The numbers sit further down, under Precautions, where stage B2 cardiomegaly is defined as meeting all three of VHS > 10.5, LA/Ao ≥ 1.6 and LVIDDN ≥ 1.7.⁷ Two of the three are echocardiographic, so a dog cannot meet the label’s definition on a radiograph alone.

Those three values are EPIC’s enrolment criteria.¹ They are not the pivotal study’s, which required LA/Ao ≥ 1.8 and set no LVIDDN threshold.⁵

The label’s numeric gate is therefore drawn from the trial that the regulator declined to treat as adequate and well-controlled, rather than from the study that supported full approval. Dogs with an LA/Ao between 1.6 and 1.8 are label-eligible and were never enrolled in 2019035. For that group the entire evidence base is EPIC.

One line has changed wording between documents, and it is worth recording because it is the only thing standing between the indication and a dog without cardiomegaly. The 2022 conditional summary said that the drug “should also not be administered to dogs before they develop cardiomegaly, as this causes an increased risk of cardiac pathology associated with exaggerated hemodynamic responses.”⁴ That sentence does not appear in the 2025 summary. The current label carries the substance in different words: “If therapy is initiated prior to the development of cardiomegaly, treated dogs are at risk for cardiac pathology associated with exaggerated hemodynamic responses to VETMEDIN.”⁷ The warning survives; only its phrasing has moved.

Its origin is the original 2007 safety package. In healthy Beagles at three and five times the label dose, pimobendan produced “severe left ventricular hypertrophy with multifocal subendocardial ischemic lesions,” “moderate to marked myxomatous thickening of the mitral valves,” and new murmurs of mitral insufficiency.⁶ At the label dose there was nothing beyond what the control dogs showed. Those findings are not evidence of harm at 0.5 mg/kg, and they are the reason the contraindication exists.

12What EPIC’s post-endpoint data can and cannot show

Two retrospective cohorts report shorter survival after heart failure in dogs treated beforehand.^{8, 9} Both are confounded by indication, and the appraisal of that question is on the gap map separately.

EPIC holds data bearing on the same question, and it has never been analysed. Of the dogs who reached the primary endpoint, 54 of 74 on pimobendan and 69 of 88 on placebo subsequently died of any cause.¹ Those are the only post-endpoint outcome figures the trial reports, and they appear as counts rather than as a time-to-event analysis.

The crude comparison cannot be interpreted, for three reasons. Pimobendan dogs reached the endpoint later, so they had less remaining follow-up before the study closed, and the two proportions are not measured over comparable time. The endpoint is a composite: roughly one dog in six reached it by dying of a cardiac cause and so has no post-heart-failure course at all, which means neither denominator is a count of dogs at risk of dying after heart failure. The difference is also nowhere near significance on the counts alone, Fisher’s exact P being 0.464, which settles nothing in either direction given the first two problems.

What can be said is narrower. EPIC’s randomised all-cause mortality curve stays favourable and does not converge toward placebo through a 365-day landmark.¹ That constitutes weak evidence against a large and persistent post-heart-failure penalty overwhelming the preclinical benefit. It does not exclude a short-lived hazard around the point of decompensation, which is what the retrospective work proposes.

The analysis that would settle it is a time-to-event comparison restricted to the dogs who reached the endpoint by developing heart failure, with time measured from that date. That analysis requires the trial’s own patient-level records rather than its published figures, so it is available to the trial holders and to nobody else. Until somebody runs it, the question stays open, and the retrospective cohorts remain the only direct evidence on it.

13Selection or harm

There is an account of the retrospective findings that requires no harm from the drug at all.

A dog that reaches heart failure despite being on pimobendan is, by definition, a dog in which the drug did not do what it was given to do. Treated dogs arriving in heart failure are therefore a selected group of non-responders. Untreated dogs arriving there are an unselected mixture of animals, some of whom would have responded had they been treated. Give both groups pimobendan at decompensation and the pretreated group does worse, because it has been enriched for animals the drug was never going to help.

The mechanism described here is a selection effect, and it would produce exactly the pattern that the retrospective studies report. It also explains the early concentration of benefit at the same time, since dogs closer to decompensation supply both most of the events and most of the opportunity to delay them.

Selection and harm make opposite predictions about one thing, which is what makes them separable:

• If the drug causes harm

The deficit should grow with exposure, so that more time on treatment produces a worse outcome afterwards.

• If it is selection

The deficit should be largest in dogs that reached heart failure quickly despite treatment, since those are the most refractory, and should shrink in dogs that stayed preclinical for years before failing.

The test is a regression of post-heart-failure survival on time to heart failure, within the treated arm. A positive slope favours selection, and a negative slope favours harm. The retrospective studies cannot do this, because the duration of preclinical treatment was not recorded. EPIC has it exactly: time to the primary endpoint is the trial’s own primary variable.

14Does the trade-off still favour treating?

If pimobendan delays heart failure but dogs then survive a shorter time after it, the question is whether the strategy still comes out ahead on total time. That question can be modelled by adding a preclinical phase to a post-heart-failure phase, taking the first from EPIC and the second from the retrospective studies.^{8, 9}

One correction is needed first. The EPIC primary endpoint is a composite, not the date of heart failure; roughly one dog in six reached it by dying of a cardiac cause and has no post-heart-failure phase at all. Adding one inflates every strategy, so the post-CHF term below is scaled by 0.833.

On that basis treating in B2 is roughly break-even once the reported post-heart-failure penalty is carried, and waiting until heart failure is clearly the worst of the three.

The answer nonetheless turns on a single choice. The preclinical advantage can be measured in two ways and the two disagree badly with each other. The area between the observed curves out to day 1570 gives 190 days, whereas the mean of a Weibull fitted to the same data and extrapolated to infinity gives 478 days. Neither figure is correct, because the first truncates the pimobendan curve while it is still at 40 per cent and therefore understates the advantage, and the second extrapolates far beyond any observed data and therefore overstates it. On the measured basis, treating in B2 loses 13 days, and on the extrapolated basis it gains 275. The comparison changes sign inside a range the trial never observed.

Break-even sits at a post-heart-failure median penalty of about 179 days on the measured basis. The reported penalties are 191 days⁸ and 269 days.⁹ On measured data the reported penalties therefore just cancel the preclinical gain, and on extrapolated data they do not come close to doing so.

The one result stable across both bases is that waiting until heart failure before starting pimobendan is the worst of the three strategies, by roughly 98 days.

This calculation is a way of framing the trade-off rather than an estimate of it. It combines three studies with different populations and endpoints, and both post-heart-failure inputs are retrospective. The analysis in section 12 would replace both of them with a randomised comparison and settle which side of break-even this falls on.

15Where this leaves it

The randomised trial provides evidence of a treatment effect, and the effect is less secure than the headline estimate suggests. Reclassifying nine dogs removes statistical significance. The proportions alone are not significant. The great majority of the absolute separation happens in the first six months.

The effect is not confined to that period, however. Restarting the clock at 23 weeks still leaves a 380-day median difference and 107 days of average event-free time gained, so dogs that were nowhere near heart failure at six months still show a benefit. That landmark comparison is computed on reconstructed curves and is not a randomised landmark analysis of patient-level data, so it cannot establish the effect with the certainty that the trial’s own data would.

The most defensible reading is that dogs approaching heart failure have the most to gain, because they have the most events available to delay, and that the trial’s statistical signal is dominated by them. Whether dogs at the mild end of B2 benefit is not answerable from the published data. EPIC found no significant treatment-by-severity interaction, but it was never powered to find one, and the absence of a detected interaction is not evidence that no interaction exists.

The regulatory record is the sharper problem. The trial was judged not adequate and well-controlled without a stated reason; the pivotal evidence is a single-arm study with no concurrent comparator and success thresholds of unexplained origin, set below the historical control rate; and the label’s numeric criteria come from the trial the regulator set aside rather than from the study that replaced it.

What would settle it. From the investigators: time from the primary endpoint to death, by randomised arm, as Kaplan–Meier curves and a Cox model; within the pimobendan arm, post-endpoint survival regressed on time to endpoint, whose slope distinguishes selection from harm; and the baseline and day-35 characteristics of dogs reaching the endpoint, by arm, day 35 being where the trial’s own longitudinal analysis finds change in heart size becomes prognostic.^{2, 3} From FDA, four questions each answerable in a sentence: which characteristics of an adequate and well-controlled study EPIC failed; whether the 80 per cent historical figure was computed on control dogs or treated dogs; how many dogs were in that historical group; and where the 54 per cent threshold came from.

—References

1. Boswood A, Häggström J, Gordon SG, Wess G, Stepien RL, Oyama MA, Keene BW, Bonagura J, MacDonald KA, Patteson M, Smith S, Fox PR, Sanderson K, Woolley R, Szatmári V, Menaut P, Church WM, O’Sullivan ML, Jaudon JP, Kresken JG, Rush J, Barrett KA, Rosenthal SL, Saunders AB, Ljungvall I, Deinert M, Bomassi E, Estrada AH, Fernandez Del Palacio MJ, Moise NS, Abbott JA, Fujii Y, Spier A, Luethy MW, Santilli RA, Uechi M, Tidholm A, Watson P. Effect of pimobendan in dogs with preclinical myxomatous mitral valve disease and cardiomegaly: the EPIC study — a randomized clinical trial. J Vet Intern Med. 2016;30(6):1765–1779. doi:10.1111/jvim.14586. PMID 27678080.
2. Boswood A, Gordon SG, Häggström J, Wess G, Stepien RL, Oyama MA, Keene BW, Bonagura J, MacDonald KA, Patteson M, Smith S, Fox PR, Sanderson K, Woolley R, Szatmári V, Menaut P, Church WM, O’Sullivan ML, Jaudon JP, Kresken JG, Rush J, Barrett KA, Rosenthal SL, Saunders AB, Ljungvall I, Deinert M, Bomassi E, Estrada AH, Fernandez Del Palacio MJ, Moise NS, Abbott JA, Fujii Y, Spier A, Luethy MW, Santilli RA, Uechi M, Tidholm A, Schummer C, Watson P. Longitudinal analysis of quality of life, clinical, radiographic, echocardiographic, and laboratory variables in dogs with preclinical myxomatous mitral valve disease receiving pimobendan or placebo: the EPIC study. J Vet Intern Med. 2018;32(1):72–85. doi:10.1111/jvim.14885. PMID 29214723.
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4. US Food and Drug Administration, Center for Veterinary Medicine. Freedom of Information Summary, original conditional new animal drug application, Vetmedin-CA1 (pimobendan) chewable tablets, application number 141-556. Conditional approval granted 16 June 2022. animaldrugsatfda.fda.gov/adafda/app/search/public/document/downloadFoi/12512
5. US Food and Drug Administration, Center for Veterinary Medicine. Freedom of Information Summary, supplemental new animal drug application, NADA 141-273, Vetmedin (pimobendan) chewable tablets and Vetmedin solution. Approved 19 December 2025. animaldrugsatfda.fda.gov/adafda/app/search/public/document/downloadFoi/17792
6. US Food and Drug Administration, Center for Veterinary Medicine. Freedom of Information Summary, original new animal drug application, NADA 141-273, Vetmedin (pimobendan) chewable tablets. Approved 30 April 2007. animaldrugsatfda.fda.gov/adafda/app/search/public/document/downloadFoi/832
7. Vetmedin (pimobendan) chewable tablets, prescribing information. Boehringer Ingelheim Animal Health USA Inc. Revised April 2026. dailymed.nlm.nih.gov
8. McAulay G, Hills M, Dukes-McEwan J, Dutton E, Jakubczak A, Singleton D, Bode E, Yangwanitset W, Hezzell M. Survival of dogs with myxomatous mitral valve disease administered preclinical pimobendan in comparison to pimobendan-naïve dogs from the onset of congestive heart failure. J Vet Cardiol. 2026;66:63–73. doi:10.1016/j.jvc.2026.05.001. PMID 42247930.
9. Park SW, Kim K, Do YJ, Lee JW, Ro WB, Lee CM. Impact of administering cardiac medication to small-breed dogs with preclinical myxomatous mitral valve disease on survival after congestive heart failure. Vet Q. 2025;45(1):2560412. doi:10.1080/01652176.2025.2560412. PMID 40975815.
10. Keene BW, Atkins CE, Bonagura JD, Fox PR, Häggström J, Fuentes VL, Oyama MA, Rush JE, Stepien R, Uechi M. ACVIM consensus guidelines for the diagnosis and treatment of myxomatous mitral valve disease in dogs. J Vet Intern Med. 2019;33(3):1127–1140. doi:10.1111/jvim.15488. PMID 30974015.

—Declarations