Classical technical analysis doctrine holds that logarithmic charts are essential for long-term price analysis, as they normalize percentage changes across time. This orthodoxy is taught in every trading textbook, embedded in every charting platform's defaults, and repeated as gospel by market technicians worldwide. It is asserted far more often than it is tested. When we tested it, we found that the doctrine is not well supported—and our own earlier claim to have overturned it has not yet been independently confirmed either.
This page previously reported that linear displacement outperformed logarithmic scaling "not marginally, but decisively." That conclusion came from anchors selected by hand, using the same recurring manual swing-selection methodology used throughout this framework—not swings chosen after the fact to flatter the result. We have since tried to re-test it with swings detected automatically instead of by hand, over 240 paired outcomes, and on that automated re-run the two methods are statistically indistinguishable (p = 0.17), with log's median error slightly lower. We have left the original figures on this page, clearly marked, rather than quietly deleting them. What we cannot yet say is why the automated re-test failed to reproduce the manual result: it may be that the original edge was an artefact of selection, or it may be that our automated swing detector is simply a poor substitute for the manual methodology it is meant to stand in for—we have not yet built a detector we can show replicates manual selection, so neither explanation is currently ruled out. Until we can, the honest position is that we use linear for the structural reasons set out in Section 8, and that Section 7 records an open discrepancy between manual and automated testing, not a settled refutation.
What does survive testing is the structure itself rather than the scale it is drawn on. Across 25 international indices and 344 resolved cases, price terminated on a Fibonacci extension level about 75% of the time against a matched-chance baseline of 54%—a result that held in every market examined. That is the claim this analysis is built on, and it is a claim about where price comes to rest, not about which axis one draws. This page presents the evidence for what I term the Bow and Arrow Effect: the principle that pullbacks do not merely interrupt trends but appear to preload the energy expenditure of the expansions that follow.
The case for logarithmic scaling in long-term chart analysis rests on a seemingly unassailable foundation. Consider: a move from $100 to $200 represents a 100% gain, identical in percentage terms to a move from $10,000 to $20,000. On a linear chart, the second move appears 100 times larger; on a logarithmic chart, both are visually equivalent. This normalization appears essential when analyzing price action across decades or centuries, where early prices are measured in tens and modern prices in thousands.
The argument proceeds as follows:
This orthodoxy is not merely conventional wisdom; it is codified in CFA curricula, endorsed by academic finance, and embedded in the technical analysis canon. To challenge it appears quixotic at best, ignorant at worst.
When we first applied anchor swing methodologies to Fibonacci extension analysis across the history of the Dow Jones Industrial Average, we believed we had found a stark divergence: that logarithmic scaling rendered the levels useless while linear scaling produced extraordinary accuracy. We described it at the time as a binary difference which the data unambiguously settled.
That was overstated, and the correction the reader needs is narrower than "it was not." The anchors in that study were the same honestly-drawn, manually-selected swings used throughout this framework, not swings chosen to fit the answer. What we have not yet managed is to reproduce that manual selection with an automated detector: when we re-ran the comparison mechanically over 240 paired outcomes, the two scalings performed the same within statistical error, and the sharp original divergence disappeared. That could mean the original divergence was an artefact of manual selection. It could equally mean our automated swing detector is a poor stand-in for the manual methodology—feed it worse swings and it will produce worse, more random-looking results on both scales, regardless of which one is actually correct. We do not yet know which explanation is right, and until we can build and validate a detector that faithfully reproduces manual selection, this should be read as an open discrepancy, not a debunking. The reader should hold that distinction in mind through Sections 2 and 3, which set out the original intuition, and should read Section 7 before deciding what to believe about it. We have left the argument standing in its original form because the reasoning behind it remains worth understanding, and because a research programme which silently edits its own history is worth nothing at all.
The heresy I propose is this: Linear displacement is not a charting preference—it is the measurement of market energy expenditure. When a market rallies 1,000 points, it expends structural energy in the form of capital deployment, order book absorption, and liquidity consumption. That energy cost is linear, not logarithmic. The buyer who moves the index from 30,000 to 31,000 expends the same dollar-weighted force as the buyer who moved it from 5,000 to 6,000—but vastly more than the buyer who moved it from 100 to 101.
Fibonacci extensions project future price targets based on the structure of prior swings. The standard ratios—1.272, 1.618, 2.618, 4.236, 6.854—are derived from the golden ratio and its mathematical relatives. These ratios are scale-invariant in theory; they should work identically on linear and logarithmic charts if market structure is truly percentage-based.
We believed, for some years, that they do not.
Applying anchor swing selection criteria by hand (major swing highs/lows, validated by volume and structure) across DJI history appeared to show:
This observation has not been confirmed by automated testing—and it has not been refuted by it either. When the anchor swings are detected by our automated method rather than drawn by hand using the framework's manual methodology, the divergence disappears: linear and log score within half a percentage point of one another on hit rate, and log's median error is the lower. That is a genuine result for the automated method as it currently stands. It is not, by itself, evidence that the manual finding was wrong, because we have not yet shown that the automated detector reproduces what a human applying the manual methodology actually selects.
The honest reading is narrower than either "confirmed" or "debunked." The manual anchors were not hand-picked to flatter the conclusion—they follow the same recurring selection criteria used across this framework, applied the same way whether or not a given case happened to support linear over log. What we have not yet done is build an automated process that provably selects the same swings a careful manual pass would, and until we do, a null result from the automated test is genuinely ambiguous: it is consistent with the original manual finding being an artefact, and it is equally consistent with the automated detector simply being a worse method for finding the swings that matter—garbage in, random-looking out, on both scales. Section 7 gives the numbers and states plainly which of those two explanations we can, and cannot, currently rule out.
The most counterintuitive finding of this work—and, unlike the linear-versus-log claim, one which has survived independent re-testing across 25 markets—is what I term the Bow and Arrow Effect. The principle is simple: the extent of a future expansion appears to be constrained by the magnitude of the preceding contraction, terminating at Fibonacci proportions of it more often than chance allows. "Constrained" is the correct word and "predetermined" is not. Roughly three quarters of resolved cases terminate on the ladder; the remaining quarter do not, and no anchor tells you in advance which quarter you are in.
Think of a drawn bow. The farther you pull the string back (the anchor swing, the pullback), the farther the arrow will fly (the subsequent expansion). In market terms:
Formalization:
Let S = anchor swing magnitude (high to low, in linear points)
Let E = subsequent expansion (low to future high, in linear points)
Observation: E / S ≈ φⁿ, where φ = 1.618 (golden ratio) and n ∈ {1, 2, 3, 4}
This relationship holds across time scales (intraday to multi-decade) and across volatility regimes.
This is not a predictive model in the deterministic sense. It does not tell you when the expansion will occur, nor does it guarantee that it will reach the full extension. What it provides is a structural map of likely resistance zones where energy exhaustion becomes probable. The market may stall at 1.618, capitulate at 2.618, or enter melt-up territory beyond 4.236—but these are the decision nodes where the bow's energy depletes.
I have analyzed 38 major crash episodes in DJI history from 1896 to 2025, ranging from the 1929 collapse to the 2020 COVID crash to the 2022 bear market. The methodology is consistent:
Results as originally published:
Two defects in the scoring, plus a limit on the anchor data, run through the numbers above; an audit of our own data found all three. They are set out here rather than buried in a footnote, because a reader who takes 95%, 84% and 74% at face value has been misled by us.
The success criterion cannot fail. A "significant price reaction" was recorded when price stalled, reversed, or broke out at a level. Those three outcomes exhaust the possibilities. A test in which every behaviour counts as a hit will register a hit at essentially any level, including levels chosen at random, and 36 of 38 is roughly what such a rule produces. That figure measures the looseness of the definition, not the significance of the levels.
Seven of the anchors are unverified, and the precision of the rest is overstated. An audit of the 38 episodes against real price data found 19 anchors matching a genuine pre-peak swing low within 1%, and 12 more matching one within 1–4%—real structure, rounded for display, not numbers reverse-engineered from the outcome. That leaves 7 open: 3 whose nearest match postdates the peak they are supposed to anchor, and 4 which the test could not match at all (one a daily-versus-weekly timeframe gap, one the 1914 exchange closure, and a probable duplicate entry counted twice). Two things follow. The unverified seven cannot be treated as evidence until they are resolved. And for the other 31, a 1–4% difference in the anchor moves the resulting ratio, so a terminal quoted as landing exactly on a level is claiming a precision the input does not support—read them as measurements with a tolerance.
The significance test used the wrong null. Scattering levels at random within the historical price range does not model the criterion actually applied. Re-scored against the real pivot nearest each stated anchor, with a matched-chance baseline, the crash population yields 24 of 38 (63%) against a 53% baseline: p = 0.13, which is not statistically significant. A size-filtered subset of larger anchor swings does show a positive lift—11 of 20 (55%) against 39%—but n = 20 will not carry the weight the original figures were made to bear.
None of this means the ladder is spurious, and none of it impugns the anchors themselves—31 of the 38 are confirmed real swings. It means that as scored here, these 38 episodes do not demonstrate the ladder: the criterion was un-failable and the null was wrong, and no anchor, however sound, rescues a test with those two properties. The evidence that does demonstrate it is cited in the abstract and rests on mechanically detected swings across 25 markets, where the anchor is fixed by rule before the outcome is known and the question of selection cannot arise at all. This section should be read as a statement of what the framework claims, not as its proof.
This page previously reported that 10,000 simulations with randomly placed extension levels gave p < 0.001 for the retracement reactions and p < 0.002 for the extension targets, and concluded: "These are not coincidences; they are structural signals." Both p-values are withdrawn. They were computed against a null that did not reproduce the permissive success criterion described above, and on a population in which several anchors remain unverified and the rest are quoted to a precision the underlying data does not support. The correct figure for this population, properly scored, is p = 0.13.
The same methodology applies to bull markets. Each major expansion from 1896 to the present (including 1921-1929, 1949-1966, 1982-2000, 2009-2022) can be described in these terms:
Consistency: The behavior is not confined to a specific era. The 1920s bull market and the 2010s bull market, separated by 90 years and orders of magnitude in absolute price, show the same proportional structure in ratio space, within the tolerances stated in Section 5. "Identical" would be the wrong word: what is preserved is the ratio at which expansions terminate, not the precision with which they do so. Measured across 25 markets, the dispersion of those terminal ratios is 0.285, against 0.450 for a matched control—tighter than chance, and a long way from exact.
A common objection to long-term technical analysis is that market structure evolves. Algorithmic trading, circuit breakers, ETFs, options gamma, high-frequency trading—surely these innovations have altered how markets move?
They have. What we observe is modal adaptation: the levels at which expansions terminate appear stable, while the microstructure around those levels—how price approaches, overshoots and returns—has changed considerably. That is the claim, and the reader should note how easily it could become unfalsifiable. If every deviation from the expected level is reclassified as an adaptation in microstructure, the framework can never be wrong about anything. Section 5.2 states the tolerance that prevents this, and it should be read as a constraint on the framework rather than as a defence of it.
| Era | Market Structure | Fibonacci Behavior | Adaptation |
|---|---|---|---|
| 1896-1929 | Specialist-driven, low volume, margin abuse | Clean reactions at extensions, minimal overshoot | — |
| 1930-1980 | Telephone orders, institutional entry, reduced leverage | Broader zones around Fib levels (±2-3%) | Volatility reduction post-Glass-Steagall |
| 1980-2000 | Electronic trading, program trading, portfolio insurance | Return to sharp reactions, flash events introduced | 1987 crash: flash to 4.236, reverse within hours |
| 2000-2025 | HFT, algorithmic dominance, options gamma, circuit breakers | Stop hunts above/below Fib levels, then reversal | Liquidity hunting: fake breaks, then snap back |
In the modern era (post-2008), we observe a recurring pattern: stop hunts just beyond major Fibonacci levels. The market will breach a 1.618 extension by 1-2%, trigger stops, absorb the liquidity, and then reverse sharply back into the Fibonacci zone. The phenomenon is real, and a model with no tolerance for it would be discarded on its first live trade.
It was previously described on this page as validation of the model. That was a mistake, and an instructive one. If a clean reaction at a level confirms the level, and a breach of the level also confirms the level, then the level is confirmed by every possible outcome and the claim has no content. Tolerance for overshoot is necessary; unbounded tolerance is an excuse. The distinction between the two is entirely a matter of saying in advance how much overshoot is permitted.
So it must be said in advance. A breach that extends no more than roughly 2% beyond the level and reverses back through it is treated here as the level holding. A breach beyond that is treated as the level failing, and the framework should be scored as wrong on that occasion. This is not a formality: our own testing records overshoots of the 6.80 extension of 16% in one cycle and 68% in another. Excursions of that size are not stop hunts and must not be filed as such. They are the level not holding, and any honest account of the framework has to record them as misses rather than reinterpret them as a subtler kind of hit.
One further caution. The explanation offered above—that algorithms hunt these levels because positioning clusters there—is plausible and unproven. We observe the price excursion. We do not observe the intent behind it, and inferring the second from the first is the same circularity discussed elsewhere in this series. The tolerance band stands on its own as a rule. It does not require the story to be true.
In October 2008, the Dow Jones Industrial Average crashed from 14,164 (October 2007) to 6,547 (March 2009), a 53.8% decline. Applying linear Fibonacci methodology:
| Level | Calculated from 2009 low | Date of Closest Approach | Price at Closest Approach | Error |
|---|---|---|---|---|
| 0.618 Retracement | 11,258 | April 2010 | 11,205 | -0.47% |
| 1.0 Retracement | 14,164 | February 2013 | 14,054 | -0.78% |
| 1.618 Extension | 18,870 | December 2014 | 18,053 | -4.33% |
| 2.618 Extension | 26,490 | January 2018 | 26,616 | +0.48% |
| 4.236 Extension | 38,820 | January 2022 | 36,953 | -4.81% |
Interpretation, with the qualifications it requires: Over a 12-year period, five major highs and resistance zones fell near linear Fibonacci extensions computed from the March 2009 low. The median error is 0.78%. The median is the flattering statistic here, and it conceals the distribution: two of the five rows—the 1.618 at −4.33% and the 4.236 at −4.81%—sit within the ±5% band used in the crash tables but outside the ±2% tolerance this framework applies elsewhere. Which convention governs decides whether they are hits or misses, and the corpus has not to date been consistent about it. Under the stricter rule they are misses, and they are recorded here as such rather than absorbed into an average.
The 4.236 row requires a further correction, and it is the one that matters. Price did not terminate at 38,820. January 2022 was its closest approach, at 36,953. The index subsequently traded far above that level—it reached 53,289 on 7 July 2026, some 37% beyond the extension—without producing the terminal the framework anticipates there. Presenting a closest approach as a hit, and ending the table at that row, gives a misleading impression of a level which was in the event passed straight through and never looked back. By the standard set out in Section 5.2, the 4.236 on this anchor is not a stop-hunt overshoot. It is a failure of the level, and the framework is scored as wrong there.
On the claim that this is not retrofitting. The arithmetic was fixed once the anchor was chosen: given 14,164 and 6,547, the extensions follow. What was not fixed in 2009 was the choice of that anchor over the several other defensible ones, the decision as to which subsequent highs count as alignments, or the tolerance within which an alignment is declared. Each was settled afterwards, with the price history visible. We hold no contemporaneous published record of these projections, and in the absence of one the honest description is a retrospective fit, presented as such. A genuine out-of-sample test of this framework requires levels published before the price arrives at them, scored on a rule fixed in advance. Section 7 is the closest thing to that test we have, and its result is far more modest than this table implies.
When the same 2008 anchor swing is analyzed using logarithmic Fibonacci extensions:
On this anchor, the logarithmic projections come in early, which is consistent with percentage compression rather than absolute displacement. The word "systematically" appeared here previously and cannot be supported by a single case. Across 240 paired outcomes (Section 7.3) log projections are not systematically early, not systematically late, and not systematically worse; their median error is in fact marginally lower than linear's. The 2008 anchor is one draw from that distribution, and it happens to favour linear. Selecting the anchor on which one's preferred method performs best, and then presenting it as characteristic, is the error this page spent its opening section accusing others of.
To compare approaches, I backtested three forecasting methods across all major DJI swings from 1950-2025:
The swings entering that comparison were identified by hand, using this framework's standing manual selection criteria. That does not by itself invalidate the results below, but it does mean they have not been independently verified by a process free of human input, and the risk is worth naming precisely: when an analyst chooses which swings count, there is a real possibility—even without any intent to do so—of unconsciously favouring the swings on which a preferred method looks right. We have not found evidence that happened here, but we also have not yet built the automated check that would rule it out. The table that follows is preserved as originally published, and should be read as unverified rather than as either confirmed or discredited.
| Method | Median Error (Highs) | Median Error (Lows) | Hit Rate (±5%) | Forecast Horizon |
|---|---|---|---|---|
| Linear Fibonacci | 2.3% | 3.1% | 78% | Months to years |
| Log Fibonacci | 11.2% | 9.8% | 34% | Months to years |
| ARIMA/GARCH | 8.7% | 7.4% | 52% | Weeks to months |
| VAR (Macro) | 15.3% | 12.1% | 41% | Quarters |
We attempted to repeat the comparison above with the analyst removed from it, using an automated swing detector instead of manual selection. Swings were detected mechanically, every detected swing was included whether or not it flattered the method, and the two scalings were scored on the same 240 paired outcomes. This automated detector has not itself been validated against the manual methodology—we do not yet know how closely the swings it finds match the ones a careful manual pass would draw—so the comparison below should be read as a test of the automated method, not as a definitive re-test of the manual one.
| Method | Median Error | Hit Rate (±5%) | N (paired) |
|---|---|---|---|
| Linear Fibonacci | 19.1% | 20.8% | 240 |
| Log Fibonacci | 14.3% | 20.4% | 240 |
Section 7 establishes that linear does not outperform log, so what follows is not an explanation of a result. It is the reason we prefer linear in spite of the absence of one. The argument is that linear displacement measures cumulative capital deployment rather than percentage return. Consider:
On this argument the market "feels" the cost of rallying 1,000 points at 30,000 as broadly similar to 1,000 points at 5,000, and the percentage difference (3.3% versus 20%) is the abstraction. The cancellation is the whole of the case for linear, and it rests on an assumption that should be visible rather than buried: that capitalisation, free float and turnover scale proportionally with the index level. Over 130 years, across changes in index composition, listing behaviour and the divisor itself, that assumption is an approximation of unknown quality. It is a reason to prefer linear. It is not a proof that linear is right, and Section 7 shows that the data do not settle the question either way.
Why Fibonacci ratios specifically? The hypothesis I advance is self-fulfilling coordination:
This is not mysticism; it is game theory. Fibonacci becomes structural not because of inherent mathematical magic but because collective belief in linear displacement creates order flow patterns that manifest as geometric regularity.
Stated this way the hypothesis is testable, and it is worth saying what would count against it. If the levels work because participants watch them, then the effect should be strongest at the ratios most widely watched—0.618, 1.618—and weaker at ratios almost nobody plots, such as 6.854. It should have strengthened as charting software spread, and it should be weaker in markets where Fibonacci analysis is rare. If instead the effect is found to be uniform across obscure and popular ratios alike, and as strong in 1910 as in 2010, then coordination is not the mechanism and something else is producing the regularity. We regard the question as open. The cross-market evidence, which finds the terminal clustering in all 25 indices tested including several with little Western technical-analysis tradition, sits somewhat awkwardly with the pure coordination story and we do not pretend otherwise.
As noted earlier, post-2008 markets exhibit stop hunts around major Fibonacci levels. This behavior deserves deeper analysis:
Provided the tolerance is fixed in advance and adhered to, this adaptation is something the model can accommodate rather than something that refutes it. It should not be described as enhancing the model, which was the previous formulation and which quietly converted a complication into a virtue. The trading implications are:
The linear heresy is less heretical than its title suggests, and more modest than this page once claimed. Linear Fibonacci extensions do not measurably outperform logarithmic ones. When we removed analyst discretion from the comparison, the two scalings became statistically indistinguishable, and log's median error was fractionally the lower. That result was not what we expected or wanted, and it is reported here because a framework that only publishes its confirmations is not a framework but an advertisement.
What survives is more interesting than what did not. Across 25 international indices and 344 mechanically detected cases, price came to rest on a Fibonacci extension level roughly 75% of the time against a chance baseline of 54%, and the effect was positive in every market examined. That is a real, replicated, cross-market regularity. It says nothing about which axis you draw it on, and it does not need to.
The argument for linear is therefore structural rather than empirical: markets are moved by capital, and capital is spent in points rather than percentages. Absorbing the supply between 30,000 and 31,000 costs what it costs regardless of where the index began the year. That reasoning rests on assumptions about capitalisation and float which are set out in Section 8 and which we have not verified over the full 130-year window. It is a good reason. It is not a result.
The Bow and Arrow Effect—that anchor swings appear to preload the extent of the expansions which follow—remains the framework's central and best-supported observation. It suggests market structure carries a form of memory, in which the magnitude of a contraction constrains the ceiling of the recovery. Why this should be so, we do not know. The coordination hypothesis in Section 8.2 is the best account we have, and its cross-market persistence in indices with little Fibonacci tradition is an argument against it.
None of this is prediction in the deterministic sense. It is structural cartography: a map of the zones where exhaustion has historically concentrated. Price stalls at these zones more often than chance allows, and it also passes straight through them, and the framework is scored as wrong when it does. A level which "cannot be ignored" whatever price does is not a level, it is a tautology. The tolerances in Section 5.2 exist precisely so that this framework can be caught being wrong, and it has been—at 6.80 in 1987 and again in 2007, by 16% and 68% respectively.
The heresy, then, is not the rejection of orthodoxy but the insistence on measurement—including, and especially, the measurement of one's own claims. Log scales are elegant and percentage-normalised. Linear displacement is what we believe the market actually pays. On the present evidence a reader who disagrees and plots in log will forecast these levels about as well as we do, and should feel no obligation to convert.
The energy cost of movement is, we think, linear. The charts we draw are too. The evidence for the ladder does not depend on our being right about that.