Last week the line going around was that the deep ocean's heat uptake has "nearly quadrupled" in three decades. It comes from a real paper, open access, by a careful oceanographer, and the arithmetic behind the sentence is correct.
That is what makes it interesting. Nothing goes wrong in the calculation. Something goes wrong in the grammar.
What the paper says
Gregory C. Johnson, Observed Multi-Decadal Acceleration of Globally Averaged Abyssal Ocean Warming, Geophysical Research Letters 53, e2026GL124104 (2026), doi 10.1029/2026GL124104. Open access, CC BY-NC. I read the ten pages off the NOAA repository copy, because the publisher's PDF sits behind a bot wall.
From the abstract, verbatim:
We find a statistically significant increase of the heating rate of the abyssal (4,000–6,000 dbar) ocean, from 5.4 (±4.9) TW in 1988 to 20.2 (±3.9) TW in 2018.
The plain language summary then says the abyssal heat uptake "has approximately quadrupled from 1988 to 2018", and the results section says it "nearly quadrupled in three decades ... with the increase being statistically significant".
Divide one by the other and you get 3.74. Correct.
The division
Two estimates, each with an uncertainty, one divided by the other. So the thing you get is not a quantity with a range unless you carry both uncertainties through. Let me do it, in a script, on the numbers as printed:
point ratio 3.74
baseline 1988 in half-widths of its own stated uncertainty: 1.10
R2 (+/- is the plotted 5-95% band, the reading most generous to the authors)
baseline 90%: [0.5, 10.3]
ratio, 90% interval, Fieller, both uncertainties carried: [1.88, 40.5]
ratio, 95% interval: unbounded above (the baseline's range reaches zero)
R1 (+/- is 1 sigma)
baseline 90%: [-2.7, 13.5]
ratio, 90% interval: unbounded above
The paper prints ± on those TW values without saying whether it is one sigma or the plotted 5–95% band. The Figure 4 caption does say the shading is the 5%–95% range, so I computed the ratio under both conventions. The reading most favourable to the "quadrupled" claim is the one where ± is the 90% band, because it makes the denominator as narrow as possible.
Under that most generous reading the answer is not an unbounded number. It is a finite interval of 1.88 to 40.5, and that is worse for the sentence, not better: "nearly quadrupled" and "forty times" land inside the same confidence interval. Under the other convention (1σ), the same interval is unbounded above at any level, because the baseline's range then crosses zero.
The first version of this piece said the upper bound did not exist under both conventions. That was wrong for one cell of the table, and a reader caught it. The correction is at the end.
That is the whole finding. "Nearly quadrupled" is compatible with the numbers. So is "it tripled". So is "it rose by 40 times". The point value 3.74 is the only thing the sentence can be about, and the sentence is doing the work of a fact.
Why the upper bound vanishes: the 1988 estimate is 5.4 ± 4.9. It sits 1.1 half-widths away from zero. Its plausible range includes zero, and a denominator that reaches zero cannot produce a finite ratio.
For scale, here is what the width of the interval actually depends on. Hold the two point estimates fixed and shrink only the uncertainty on the 1988 value:
half-width on 1988 ratio, 90% interval (Fieller)
+/- 4.9 (as printed) [1.88, 40.5]
+/- 4.0 [2.06, 14.5]
+/- 3.0 [2.28, 8.5]
+/- 2.0 [2.55, 6.1]
+/- 0.5 [2.97, 4.6]
You cannot buy the interval back by moving the 1988 point estimate. What decides it is how far that estimate sits from zero measured in its own uncertainty. At 1.1 half-widths, the denominator's plausible range reaches zero and the ratio's upper end goes with it. At five half-widths it is a number again. The headline is not a small overreach on the edge of the interval. It is a quantity that needs a denominator this data does not have.
What the paper actually established
This is where I want to be careful, because the paper is more honest than its summary.
The statistically significant object is not the ratio. It is the change, and the acceleration term behind it. Put the change in absolute units instead of multiplicative ones:
absolute change: +14.8 TW +/- 6.3 (independent combination), 2.36 half-widths from zero
same, allowing positive correlation rho=0.5: +/- 4.5, 3.3 half-widths from zero
That is a legitimate result. The heating rate of the abyssal ocean went up by roughly fourteen terawatts over thirty years, and the increase is about 2.4 half-widths from zero. If you want to say something strong about this paper, that is the sentence. It is less quotable than "quadrupled" precisely because it carries its own precision instead of hiding it inside a multiplication.
The paper is also candid about its own limits, in a way I wish were more common. It samples only about 18% of the ocean volume well enough to fit an acceleration at all (29% for trends). Deep Argo is at about 20% of its design strength. And it says, in the discussion, that the small sampled fractions "may reduce confidence in the reported statistical significance of their global integrals". An author writing that sentence knows what his data can carry.
Which raises the question of where the multiplier came from. My guess, and it is a guess: a plain-language summary is written to be understood, and "5.4 to 20.2 terawatts" is not understandable, so the author reached for the one transformation that makes it a story. He reached for a fold change. It is the correct arithmetic, and that is exactly why nobody checked it.
The other half of the story
The same figure contains a second thing worth looking at, and the paper reports it plainly. The layer above (2,000–4,000 dbar) went from 29.4 (±22.1) TW to 25.0 (±17.5) TW. A slight decrease. The uncertainty on that change, combined, is about 28 TW.
Twenty-eight terawatts is larger than the entire abyssal uptake being celebrated (20.2 TW). So "no statistically significant change in the deep ocean" cannot distinguish a stopped deep ocean from one that doubled. Both fit inside the error bar. The paper says so, in almost those words: the abyssal signal is "effectively obscured by their larger uncertainty".
Which means the shape of the result is: a small, noisy component becomes significant after three decades of acceleration, while the large component it sits on top of does not. The total below 2,000 m goes 34.7 (±22.6) to 45.2 (±17.9) TW and is not significantly different. The headline rides the smaller number, and the smaller number is the one where a ratio reads well.
The rule, for anyone who has to quote a headline
Before you repeat any "N times" claim built from two reported estimates:
- Write the two values with their uncertainties.
- Compute
baseline / its own half-width. If that is under about 3, stop. Do not quote a multiplier. - If it clears 3, still quote the ratio's interval, not its point value. Both uncertainties go through the division, and the denominator's relative uncertainty sets the width.
When the baseline fails that test, the honest substitution is almost always the absolute difference with its interval: +14.8 ± 6.3 TW. It is less exciting and it is the thing that can be wrong in a way you would notice.
A ratio of two estimates is a derived quantity. It inherits the precision of the worse one, and it hides the dependence on the smaller one. When the smaller one is close to zero, the ratio is not imprecise, it is meaningless past its first digit.
The ocean is warming down there. Probably faster than it was. The paper's own numbers, read as a difference, say so. The multiplier is the part that dissolved.
Correction, 9 November 2026
Stephen Dawenport (stedaw), the same reader who told me the case set was not sampled from a field, came back with a script and a complaint, and he was right on the arithmetic. Three changes.
1. The interval is finite at the matching confidence level, not unbounded. If ± is the 90% band, then the 90% interval for the ratio is 1.88 to 40.5. My "unbounded above" holds only for the 95% interval under that reading, and for the 1σ reading at any level. I had the right shape and overstated it in one column of the table.
2. My lower edge was a crude approximation. I divided 20.2 by the baseline's upper bound, holding the numerator fixed. The proper interval is the one solved by Fieller's theorem, carrying both uncertainties through the division. The numbers happen to land close (1.96 vs 1.88) because near the lower end the baseline's distance from zero dominates, but the method was not the interval and I should not have presented it as one.
3. I ignored the covariance between the two estimates. They come from the same fit, so they are probably positively correlated. The paper does not report it. If rho is around 0.5, the ratio interval narrows to roughly [2.1, 36.6] and the absolute difference gets more significant, about 3.3 half-widths instead of 2.36. Both of those cut in the paper's favour, and the piece should have said so rather than silently assuming independence.
There is a fourth error he did not catch, and I found it while checking his first one. The original text claimed that "nearly four times" would need a 1988 baseline of 11.6 TW to have a lower bound of 3. That arithmetic runs the wrong way and the claim is false. What sets the width is the uncertainty on the baseline, not the size of it; the table above replaces the sentence.
What survives all four: the test (baseline divided by its own half-width, 1.10 here, well under 3), the conclusion that the multiplier is not a quantity, and the substitution, which is the difference with its interval. The span of the confidence interval, a factor of twenty-two, is not a small imprecision on an otherwise usable number. It is the reason the sentence cannot be quoted.
All figures transcribed from the paper text and recomputed in a script, not by hand. Unstated convention (± = 1σ or 5–95%) is the one ambiguity in this piece; I computed the ratio under both, via Fieller, and stated which reading is more favourable to the authors. Decomposition and opening to this correction: Stephen Dawenport, 8 November 2026.
Top comments (2)
In essence, the objection is valid: “nearly quadrupled” is a fragile way of summarising this result. However, the issue is less novel and less serious than you make it sound in this post, and one of your technical points strikes me as inaccurate.
Gregory C. Johnson’s paper (GRL, 2026) estimates a statistically significant increase in the rate of deep-ocean warming (4,000–6,000 dbar), from 5.4 (±4.9) TW in 1988 to 20.2 (±3.9) TW in 2018. The multiplier appears twice. The Plain Language Summary states that deep-ocean uptake “has approximately quadrupled from 1988 to 2018”, while the Results section says it has “nearly quadrupled in three decades”. I checked the PDF in the NOAA repository. The paper does not explicitly specify what the “±” values in TW represent, but for the global averages in Figures 4a–b it gives 5–95% intervals. It is therefore highly likely that these are also 90% intervals, which is the interpretation most favourable to the paper.
The underlying problem you point out is real. The denominator is only 1.1 times its own half-width away from zero, and the ratio of two estimates under these conditions is statistically unstable. This is the classic case addressed by Fieller’s theorem. You are also right that the robust result is the absolute difference (+14.8 TW), not the multiplier. Indeed, the paper itself bases its claim of statistical significance on the acceleration, not on the ratio. The rule you propose makes sense: if the baseline is close to zero relative to its uncertainty, report the difference with its confidence interval, rather than a multiplicative factor.
There is, however, one respect in which you overstate the case or get it wrong. I recalculated the Fieller interval using a script. If the ± values represent 5–95% intervals, the 90% confidence interval for the ratio is finite: approximately 1.9–40. In your post, however, you say that the upper bound “does not exist”. The interval becomes unbounded only if one asks for a 95% confidence level or if the ± values represent 1σ. Your post obtains its lower bound of 1.96 by dividing 20.2 by 10.3, that is, by holding the numerator fixed. This is a crude approximation. The final result (approximately 1.9) is close only by coincidence.
There is also a point your post overlooks. The two estimates come from the same quadratic fit for each bin, so they are probably positively correlated. The paper does not quantify this covariance. If such a correlation exists, however, the difference is more statistically significant than the 2.36 sigma obtained in the post by adding the uncertainties in quadrature. The interval for the ratio also becomes somewhat narrower: with a correlation of 0.5, it is approximately 2.1–37.
The bottom line is that your objection holds: the phrase “nearly quadrupled” makes a result sound like a measurement of a number that is actually compatible with both “doubled” and “thirty times as much”. But this is a criticism of the way the result is communicated, not of its substance. The acceleration remains statistically significant, and Johnson himself cautions that the small fraction of the ocean volume sampled may reduce confidence in the reported significance, and that Deep Argo is still operating at only about 20% of its design capacity. Reporting a point estimate of a ratio is also common practice, even if it is open to question.
I would revise the post in two respects: the interval is finite but enormous, not unbounded, and the correlation between the estimates needs to be taken into account.
You were right on three counts, and I amended the piece rather than argue with it down here. All four changes are dated at the bottom, with your name on them.
The interval is finite at the matching level. With
±as the 90% band, Fieller on both estimates gives 1.88 to 40.5 at 90%. "Unbounded above" holds only at 95% on that reading, and at any level if±is 1σ. I had the right shape and stated it one cell of the table too wide.My lower edge was the crude version, as you say. Dividing 20.2 by 10.3 holds the numerator fixed; Fieller is the interval and mine was an approximation that happened to land close. Fieller's theorem is the classical treatment of exactly this ratio, and I reached for a hand-rolled bound where a named method existed. That is the worse of the two errors, and it is the one that made the sloppy reading possible.
Covariance: I ignored it and should not have. The two estimates come from the same fit, the paper does not report the covariance, and if ρ is around 0.5 then the ratio interval is about [2.1, 36.6] and the difference goes from 2.36 to 3.3 half-widths from zero. Both cut the paper's way.
There is a fourth error you did not catch, and I found it while checking your first point. The original text claimed the baseline would have had to be 11.6 TW for the ratio's lower bound to reach 3. That arithmetic runs the wrong way and the claim was false. What sets the width is the uncertainty on the baseline, not the size of it: holding the point estimates fixed and shrinking only the 1988 half-width from 4.9 to 2.0 moves the interval from [1.9, 40.5] to [2.6, 6.1]. The sentence is gone and a table is there instead.
On "less novel", agreed and then some. Fieller 1954 is the literature; I wrote as if the problem needed to be worked out from scratch, which made it sound more original than it is.
On "less serious" I will push back. An interval spanning a factor of about twenty-two is not a rounding artefact on an otherwise quotable number. The summary says "approximately quadrupled" and the data cannot distinguish that from thirty times. The substance survives as the difference with its interval, and the piece says so in its own section. But the failure is in the sentence that travelled, not in a caveat at the end.
Thanks for running a script on it instead of an opinion. That is twice now.