The Measurement Problem in Crypto Research
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Why Most Bitcoin Indicators Fail Validation, and What It Takes to Build Crypto Research That Survives Being Checked
A structural analysis of the validation gap in digital asset analytics: why the standard analytical toolkit produces findings that cannot survive an honest baseline, what four specific failure modes generate false results, and what a research stack must expose before its outputs deserve institutional weight.
There is a category error at the centre of most digital asset research, and it is not a matter of sophistication. It is a matter of what question the analysis is answering.
The dominant mode of crypto analysis is descriptive. An indicator fires; price subsequently rises; the indicator is credited. This is not fraud and it is rarely even conscious. It is the natural output of an analytical culture that has inherited the visual grammar of technical analysis without inheriting the validation apparatus that any other quantitative discipline would require before publishing a claim.
The problem is that Bitcoin rose enormously over the period every one of these indicators is tested on. An asset that compounds at the rate Bitcoin has compounded makes almost any long-biased rule look prescient. Buying on a randomly chosen day since 2010 returned approximately 96 per cent over the following year. An indicator followed by a hundred per cent gain has, against that benchmark, discovered nothing whatsoever.
Almost no published crypto analysis reports that benchmark. This single omission is responsible for more false confidence in this asset class than any deliberate misrepresentation.
What follows is a structural argument about why this happens, what specific mechanisms generate false findings, and what a research stack must expose before an institutional reader should assign weight to its outputs. It is grounded in a concrete exercise: over the past several weeks I rebuilt the Crypto Exponentials research suite from the data layer upward, subjected every claim in it to independent recomputation, and in the process discovered a methodological error in my own work that had produced a published finding which did not survive correction. That correction is documented in Part V, not because self-criticism is charming, but because the willingness to publish it is the only credential a research product genuinely has.
Part I: The Miscalibration, Two Layers Deep
The first layer of miscalibration is the absence of a counterfactual.
When an analyst reports that Bitcoin rose 112 per cent in the year following some condition, the implicit claim is conditional: given this signal, returns were elevated. But a conditional claim requires an unconditional comparison. What did the year following a randomly selected day produce? Without that number, the reported figure is not evidence about the indicator. It is evidence about the asset.
This is not a subtle point, and it is not new. Brock, Lakonishok and LeBaron established the framework for evaluating technical trading rules against unconditional benchmarks in equity markets more than three decades ago, and Sullivan, Timmermann and White subsequently demonstrated that the apparent profitability of those same rules largely dissolved once data-snooping was properly accounted for. The infrastructure for doing this correctly has existed since the 1990s. Digital asset research has largely not adopted it.
The second layer of miscalibration is deeper and almost entirely absent from crypto analytics: the sample is far smaller than the observation count suggests.
A forward-return study on daily Bitcoin data will report sample sizes in the thousands. A state that has persisted across 2,400 days will be described as 2,400 observations. But those observations overlap. The one-year forward window of a day in January shares 364 days of price path with the window of the day that follows it. They are not independent draws from a distribution. They are one draw, measured 365 times.
The effective sample is not thousands. Across fifteen years, Bitcoin has produced roughly four market cycles. Four. Every claim about what “usually” follows a condition in Bitcoin is a claim resting on approximately four independent episodes, however many rows the table contains.
Once both layers are taken seriously, most published crypto findings do not survive.
Part II: The Baseline Test, Applied
To make the argument concrete rather than rhetorical, I tested the eight most widely quoted technical rules in Bitcoin against the unconditional baseline, over the full daily history from 2010.
The methodology is deliberately unremarkable. Each rule’s trigger is defined precisely enough to be coded. Triggers within ninety days of one another are counted once for the slower rules and thirty days for the MACD, which fires far more often. Forward returns are simple price changes. The comparison is the median return following a trigger against the median return following any day in the same history.
The results:
| Rule | Triggers | 1 month | 3 months | 1 year | Verdict |
|---|---|---|---|---|---|
| RSI crosses above 70 | 38 | +8.9 | +26.2 | +56.0 | Evidence of a difference |
| RSI crosses below 30 | 29 | −2.7 | +6.2 | −19.5 | No clear evidence |
| Bollinger width compression | 25 | −4.7 | −5.3 | −19.1 | Evidence against |
| Realised volatility compression | 27 | −8.5 | −9.6 | +13.7 | No clear evidence |
| Golden cross (50d above 200d) | 12 | −4.8 | −0.9 | +5.1 | No clear evidence |
| Death cross (50d below 200d) | 13 | −5.3 | +14.0 | −79.8 | No clear evidence |
| MACD crosses above signal | 114 | +0.8 | +2.4 | −11.2 | No clear evidence |
| MACD crosses below signal | 112 | +0.5 | −3.4 | −14.6 | No clear evidence |
Figures are percentage-point differences from the unconditional baseline over the same horizon.
Three observations follow.
The MACD, on the largest samples available, found nothing. Over 110 triggers in each direction, the difference from a randomly chosen day at one month is +0.8 and +0.5 percentage points. That is not a weak signal. It is the absence of one, on the sample most likely to detect a real effect if it existed.
The golden cross underperforms at short horizons. Minus 4.8 percentage points at one month, on twelve triggers in fifteen years. This is not a defect in the indicator; it is what a lagging indicator does. A fifty-day average clearing a two-hundred-day average is an arithmetic consequence of a move that has already happened. It becomes a problem only when it is marketed as anticipation.
The one rule that separates from the baseline is inverted relative to its own textbook. RSI crossing above seventy — the level taught as a signal to reduce exposure — was followed by returns ahead of the baseline, with confidence intervals excluding zero at one month and three months. At one year the interval includes zero, so the effect is a near-term phenomenon rather than a durable edge.
The honest interpretation of that last result is deflationary rather than exciting. Momentum extremes cluster inside strong trends; the finding is probably a restatement of trend persistence rather than a discovery about the oscillator. It is not a trading rule. It is evidence that a rule widely followed in the opposite direction has no historical support for being followed in that direction, which is a different and more useful claim.
Part III: Four Mechanisms That Manufacture False Findings
The failures above are not random. They arise from four specific mechanisms, each of which is well documented in the broader quantitative finance literature and each of which is endemic in digital asset analytics.
Mechanism one: look-ahead contamination in historical classification
The most insidious failure is not using tomorrow’s price to predict tomorrow’s price — nobody does that consciously. It is using parameters estimated over the full sample to classify historical states, then measuring what followed those states.
Consider a model that ranks each historical day as cheap or expensive relative to a fitted trend. If the trend is fitted once, over all available data, then the classification of a day in 2015 depends on prices from 2023. No participant in 2015 could have known that day was “cheap” by that definition. Any forward-return statistic conditioned on that classification is contaminated, and the contamination flows in the direction of making the classification look more informative than it was.
This is a specific instance of the general problem Bailey and López de Prado formalised as backtest overfitting, and it is far more common than deliberate curve-fitting because it does not feel like a modelling choice at all. It feels like data preparation.
Mechanism two: overlapping windows presented as independent observations
Discussed in Part I. Its practical consequence is that standard confidence intervals, which assume independent draws, are dramatically too narrow. A result that appears to exclude zero under an independence assumption frequently includes zero once the dependence structure is respected.
The correct treatment is a block bootstrap — resampling contiguous stretches of the time series rather than individual observations, so that the local dependence structure is preserved in each replicate. Künsch established the method; Politis and Romano extended it. Applying it to crypto forward-return studies is neither difficult nor common.
Mechanism three: specification search presented as discovery
The number of plausible technical rules is effectively unbounded. Vary the lookback, vary the threshold, vary the smoothing, vary the confirmation condition, and a single indicator becomes a family of hundreds. Test enough of them against a single price history and some will appear to work at conventional significance levels purely by construction.
Harvey, Liu and Zhu made the definitive statement of this problem for the equity anomaly literature: given the number of factors that have been tested, the conventional significance threshold is far too permissive, and a substantial fraction of published findings are likely false. The digital asset literature has run the same search across a shorter history with less discipline and less disclosure.
The defence is not statistical; it is procedural. Specifications must be fixed before testing, the number of specifications tested must be disclosed, and rules that failed must remain visible rather than being quietly dropped.
Mechanism four: refitting a failed model and presenting the refit as the original claim
When a published model diverges from reality, the natural response is to re-estimate its parameters on the new data. This is legitimate as a modelling exercise and illegitimate as a defence of the original claim, because it silently replaces a falsifiable prediction with a descriptive fit.
The stock-to-flow model is the canonical example in this asset class. The published specification implies a Bitcoin value around $745,000 today; the actual price is approximately eleven per cent of that. A full-sample refit produces a better-looking chart while concealing a structural break after May 2021 that no parameter adjustment removes. Presenting the refit without the original is not analysis. It is the preservation of a conclusion after its supporting argument has failed.
Part IV: What This Means for the Standard Toolkit
Applying the four mechanisms to the analytical vocabulary in common use produces an uncomfortable inventory.
Halving-cycle analysis rests on four completed windows. Four. The multiples have compressed sharply across them — approximately ×91, ×29, ×8.3, and ×2.0 so far — and it is entirely reasonable to describe that compression. It is not reasonable to extrapolate it, and the honest presentation states the sample size adjacent to the chart rather than in a footnote. A further complication rarely acknowledged: defining cycles halving-to-halving places the 2020 window’s peak in March 2024, not at the celebrated November 2021 top. The narrative and the arithmetic disagree, and which one an analyst uses is itself a discretionary choice affecting the result.
Market-phase labels — bull, bear, sideways — are descriptive rather than predictive, and testing them establishes this clearly. Classifying each day by drawdown and trend, days labelled as drawdown were followed by a median +112 per cent over the following year; days labelled as advance, +18 per cent. The comfortable label has historically been the worse entry by a factor of six. The label is also late by construction, since a drawdown cannot be declared until price has already fallen substantially, and unstable, flipping within thirty days on approximately thirteen per cent of days even with hysteresis applied.
Chart-pattern methods — Fibonacci retracements, trend lines, most candlestick formations — cannot be evaluated at all, and this deserves stating plainly rather than diplomatically. Their levels depend on which swing points the analyst selects. Change the selection and every level moves, which means no rule exists that can be coded, run over the history, and scored. This is not an argument that they are worthless to a discretionary trader. It is an argument that they cannot appear in a research product that claims its outputs are testable, because there is nothing to test.
Entity-adjusted on-chain metrics present a subtler version of the same problem. The adjusted variants of SOPR, realised cap and holder cohorts depend on proprietary address clustering that cannot be independently verified. An analyst using them is asserting a conclusion that rests on a vendor’s unpublished heuristics. The defensible choice is to publish the unadjusted figure, state that its level is not comparable to the adjusted version, and let the reader weigh the gap.
Part V: The Error in My Own Work
The argument above is easy to make about other people’s research. Its credibility depends on whether it is applied to one’s own.
During construction of the market-context page in the suite described in Part VII, I built a composite that ranks Bitcoin against its own history on three lenses: market value to realised value, the Mayer multiple, and deviation from a power law in time. Each percentile was computed as of the relevant day, using only prior observations — the discipline described in Part III, mechanism one.
Except for one of them. The power-law deviation was measured against a trend fitted over the entire sample. Coefficients estimated from later years were therefore participating in the classification of earlier days, and those classifications drove a forward-return table published on the page.
I found this during a review pass and corrected it: the trend is now fitted on an expanding window, using only data available up to each day.
The correction changed the result. The cheapest decile of days had shown a median one-year forward return of +61 per cent. Computed without contamination, it shows +14 per cent, with a confidence interval spanning −46 to +117 per cent — an interval that comfortably includes zero. A finding the page had reported as real was an artefact of my own methodological error.
Two further corrections in the same review are worth recording, because both were the kind of defect that survives casual inspection. The threshold table, which purports to state the levels at which each lens would read differently, was searching historical observations for whichever value happened to be ranked near the target percentile — a different quantity from the quantile of the reference distribution, and not the number the table claimed to show. And the confidence intervals themselves, which I had described as a moving-block bootstrap, were initially resampling filtered observations rather than contiguous calendar blocks. Both are now implemented as described.
None of this is presented as unusual diligence. It is the minimum standard, and the reason to publish it is structural: a research product’s only genuine credential is the record of what it got wrong and how the error was found. A methods page that contains no corrections is either very new or not being read by its author.
Part VI: What a Research Stack Must Expose
If the failures are systematic, the remedy is architectural rather than analytical. The following are not aspirations; they are the minimum disclosures that allow an external reader to evaluate a claim rather than accept it.
The unconditional baseline, adjacent to every conditional claim. Not in the methodology, not on request. In the same table, in the same row.
Effective sample size, distinguished from observation count. State the number of rows and the number of independent episodes. Where windows overlap, say so where the number appears.
Interval estimates produced by a method appropriate to dependent data. A point estimate without an interval is a claim without a strength. A block bootstrap, seeded so results are reproducible, and run under multiple seeds where the interval is itself unstable.
Point-in-time integrity, asserted specifically. Not “this analysis avoids look-ahead” but a statement of what information each historical classification used and when it became available.
The specifications that failed, retained and visible. A model page showing only the specification that worked is a filtered result. The rejected variants and the reason for rejection belong in the same document.
Falsification conditions defined in advance. For each model, the observable conditions under which it should be considered broken, stated before they occur and monitored continuously. A status derived from those conditions is a statement about breakdown, not about validity, and should be labelled accordingly.
Data provenance to the field level. Source, series identifier, observation date, transformation applied, and whether the figure is measured or derived. Where a quantity is reconstructed rather than read directly — realised capitalisation recovered from market capitalisation and MVRV, for instance, rather than rebuilt from the UTXO set — that reconstruction belongs in the disclosure, because it determines what the number can support.
Coverage gaps named rather than interpolated. Of eleven US spot Bitcoin ETF issuers, four publish machine-readable daily holdings. The correct treatment is to measure those four, state the coins covered and the share of supply, and name the seven that do not publish with the reason for each. The incorrect treatment — inferring the missing issuers from assets under management and price — produces a complete-looking number that is partly estimate presented as measurement.
No composite score. This is the most frequently violated principle and the most consequential. Three valuation lenses currently disagree by thirty-four points on a hundred-point scale on the site described below: one reads cheap, two read average. That disagreement is information about the state of the evidence. Averaging it into a single confident number destroys precisely the signal that a sophisticated reader needs.
Part VII: The Architecture, as Instantiated
The principles above are not hypothetical. The Crypto Exponentials research suite implements them across eleven surfaces, and the specific structure is offered here as one worked example rather than as a template.
The data layer is a public snapshot: eleven sources, refreshed daily, published as plain JSON with a manifest recording the status and through-date of every series. It is a repository anyone can read or build on. No keys, no gating, no proprietary transformation between source and publication.
The valuation layer implements three independent models — a Metcalfe-style network valuation using cumulative address stock as a user proxy, a power law in time, and realised value — each publishing its out-of-sample error rather than only its central estimate. The Metcalfe page carries two calibrations with an explicit distinction between the reference specification retained for comparability with published estimates and the specification the validation prefers, because these differ materially and a reader should not have to reconstruct which is which.
The market-state layer covers flows, positioning, options and mining economics: estimated ETF flows derived from four issuers’ own holdings disclosures covering approximately 866,790 BTC, the twenty-five-delta risk reversal and at-the-money implied volatility from the listed option chain, CFTC leveraged-fund positioning with the column mapping verified against the report’s own internal arithmetic, and the fee share of miner revenue that must rise as the subsidy declines.
The validation layer is the part that distinguishes the exercise. One page tests the famous indicators — Pi Cycle, stock-to-flow, the two-year moving-average multiplier, the two-hundred-week moving average — publishing every historical trigger and what followed. Another tests the standard technical toolkit against the unconditional baseline, as reproduced in Part II. Both state their sample sizes prominently and neither reports a result without its interval.
The synthesis layer places price against its own record on three lenses simultaneously, publishes the historical distribution of what followed comparable readings with block-bootstrap intervals, states which lenses disagree and by how much, and declines to produce a recommendation.
The governance layer is a methods document recording every model specification, every independent reconciliation, every rejected variant, and every correction with the before-and-after numbers. It opens with a current build status so that live state is not confused with historical changelog entries.
What the suite deliberately does not contain is as significant as what it does: no composite score, no probability of a bull market, no price target, no buy, hold or sell indication. That last omission is not caution. It is a statement about what the data can support. A recommendation depends on time horizon, position size, tax circumstance, and whether a deep drawdown would force liquidation at the worst moment — none of which are observable in market data. Two readers facing identical readings should rationally act differently, and any single label printed for both is a fiction.
Part VIII: What an Institutional Reader Should Demand
For allocators, analysts and researchers evaluating any digital asset research product, including this one, the following questions separate testable work from decorated description.
What is the unconditional benchmark, and is it displayed? If a conditional return is reported without the unconditional comparison, the finding is uninterpretable regardless of its magnitude.
How many independent episodes support the claim? Not observations. Episodes. If the answer is four, the correct response to any confident extrapolation is scepticism.
What information did the historical classification use, and when was it available? The specific question that detects look-ahead contamination. A vague assurance is not an answer.
How many specifications were tested before this one was published? If the number is unknown or undisclosed, the reported significance is not the true significance.
What would falsify this model, and is that condition monitored? A model without stated breakdown conditions cannot be evaluated, only believed.
Where is the list of things this product got wrong? If it does not exist, either the product is new or its errors are being absorbed rather than published. Both are informative.
What is measured, and what is estimated? The distinction should be visible at field level, not inferable from methodology prose.
Where does the evidence disagree with itself? A product that always presents a coherent view is either extraordinarily fortunate or is suppressing the disagreement. Disagreement is the normal state of independent measurements and its absence deserves explanation.
Part IX: Failure Modes of Research Products Themselves
Research infrastructure has its own characteristic failures, distinct from the analytical ones, and they are worth naming because they arrive later and are harder to see.
Feature accretion under the guise of thoroughness. Every additional indicator increases surface area, dilutes the reader’s attention, and raises the probability that some displayed number is wrong and unnoticed. A stack of thirty indicators is not more rigorous than a stack of eight; it is less maintainable and more likely to contain an error nobody has checked in months. The discipline that matters is the willingness to decline additions that cannot be validated.
The drift toward the composite. The commercial pressure to produce a single number is relentless, because a single number is shareable, screenshot-friendly and easy to build a following around. It is also the point at which a research product becomes a signal service, and the moment that happens the entire body of work is judged by whether last month’s number was right.
Governance theatre. Model registries, version identifiers, audit trails and reproducibility packages are valuable when they serve an actual reader with an actual question. Constructed in advance of that reader, they consume the effort that should have gone into correctness and produce the appearance of rigour rather than the substance. The correct sequence is: get the numbers right, publish the errors, and add governance apparatus when someone asks a question it would answer.
Rendering fragility. A research site that computes its figures client-side presents nothing at all to a reader without JavaScript, to assistive technology, or to an automated consumer. The mitigation is not necessarily server-side rendering of every chart; it is ensuring the underlying data is reachable in a plain format and saying so on the page.
The Synthesis
The argument of this piece can be stated compactly.
Digital asset analysis has inherited a visual and rhetorical toolkit without inheriting the validation apparatus that would make its outputs evidential. The consequence is a body of published research in which conditional claims are made without unconditional benchmarks, sample sizes are reported as observation counts rather than independent episodes, historical classifications are contaminated by parameters estimated from later data, and failed specifications are quietly refitted rather than reported as failures.
When the standard toolkit is subjected to the baseline test, most of it does not survive. The MACD, on the largest available sample, produces differences from a random day of under one percentage point. The golden cross underperforms at short horizons. Stock-to-flow is off by an order of magnitude and cannot be rescued by refitting. The market-phase label most readers want is nearly inverted as a forward indicator. The single rule that separates from the baseline does so in the direction opposite to its own textbook, and probably only restates trend persistence.
These are not arguments that Bitcoin cannot be analysed. They are arguments that the analysis must be built differently: with the counterfactual displayed beside every claim, intervals produced by methods appropriate to dependent data, point-in-time integrity asserted specifically rather than generally, failed specifications retained in public, and no composite that averages away the disagreement between independent measurements.
The final principle is the one that matters most and is hardest to institutionalise. A research product’s credential is not the sophistication of its models or the breadth of its coverage. It is the record of what it got wrong, how the error was detected, and what changed as a result. I published a finding that turned out to be an artefact of my own look-ahead contamination, and correcting it reduced a reported +61 per cent to +14 per cent with an interval spanning zero. That correction is on the methods page with both numbers.
Any research product that has been running long enough and is being read carefully enough will have such a record. If it does not, that absence is the most informative thing about it.
The tools discussed throughout are free, require no registration, and compute their figures in the reader’s browser from a public data snapshot that anyone can inspect or rebuild: cryptoexponentials.com/tools. The data layer is open at github.com/akpasz/btc-data. Corrections are welcome and will be published.
Research and Reference Foundation
The following works inform the analytical framework developed in this piece.
On evaluating trading rules against unconditional benchmarks
Brock, W., Lakonishok, J., and LeBaron, B. (1992). Simple Technical Trading Rules and the Stochastic Properties of Stock Returns. Journal of Finance, 47(5), 1731–1764. The foundational treatment of technical rule evaluation against unconditional return distributions.
Sullivan, R., Timmermann, A., and White, H. (1999). Data-Snooping, Technical Trading Rule Performance, and the Bootstrap. Journal of Finance, 54(5), 1647–1691. Demonstrates that apparent technical rule profitability largely dissolves once the universe of tested specifications is accounted for.
White, H. (2000). A Reality Check for Data Snooping. Econometrica, 68(5), 1097–1126. The formal framework for testing whether the best-performing rule in a searched universe outperforms by more than chance.
On backtest overfitting and specification search
Bailey, D., Borwein, J., López de Prado, M., and Zhu, Q. (2014). Pseudo-Mathematics and Financial Charlatanism: The Effects of Backtest Overfitting on Out-of-Sample Performance. Notices of the American Mathematical Society, 61(5), 458–471. The definitive treatment of how specification search generates spurious backtest performance.
Harvey, C., Liu, Y., and Zhu, H. (2016). …and the Cross-Section of Expected Returns. Review of Financial Studies, 29(1), 5–68. Establishes that conventional significance thresholds are far too permissive given the number of factors tested in the published literature.
López de Prado, M. (2018). Advances in Financial Machine Learning. Wiley. Includes the most practical treatment of overlapping-sample problems and their consequences for inference in financial time series.
McLean, R.D. and Pontiff, J. (2016). Does Academic Research Destroy Stock Return Predictability? Journal of Finance, 71(1), 5–32. Empirical evidence on post-publication decay, directly relevant to the durability of any published indicator.
On resampling methods for dependent data
Künsch, H.R. (1989). The Jackknife and the Bootstrap for General Stationary Observations. Annals of Statistics, 17(3), 1217–1241. The origin of the block bootstrap and the correct starting point for inference on overlapping financial windows.
Politis, D. and Romano, J. (1994). The Stationary Bootstrap. Journal of the American Statistical Association, 89(428), 1303–1313. Extends block resampling with randomised block lengths, addressing sensitivity to block-length choice.
Diebold, F. and Mariano, R. (1995). Comparing Predictive Accuracy. Journal of Business and Economic Statistics, 13(3), 253–263. The standard framework for testing whether one forecast genuinely outperforms another.
On out-of-sample evaluation and the limits of in-sample fit
Meese, R. and Rogoff, K. (1983). Empirical Exchange Rate Models of the Seventies: Do They Fit Out of Sample? Journal of International Economics, 14(1–2), 3–24. The canonical demonstration that strong in-sample fit routinely fails out of sample, and the intellectual template for validation-first research.
Campbell, J., Lo, A., and MacKinlay, A.C. (1997). The Econometrics of Financial Markets. Princeton University Press. The standard reference for the statistical treatment of return predictability and its pitfalls.
Ioannidis, J. (2005). Why Most Published Research Findings Are False. PLoS Medicine, 2(8), e124. Although written for biomedical research, the structural argument about prior probability, sample size and researcher degrees of freedom transfers directly.
Leamer, E. (1983). Let’s Take the Con Out of Econometrics. American Economic Review, 73(1), 31–43. On specification sensitivity and the necessity of reporting how results vary across defensible modelling choices.
On digital asset market structure and valuation
Liu, Y. and Tsyvinski, A. (2021). Risks and Returns of Cryptocurrency. Review of Financial Studies, 34(6), 2689–2727. The most rigorous academic treatment of the cryptocurrency return distribution and its factor structure.
Makarov, I. and Schoar, A. (2020). Trading and Arbitrage in Cryptocurrency Markets. Journal of Financial Economics, 135(2), 293–319. On market fragmentation, price divergence across venues, and the practical limits of arbitrage.
Peterson, T. (2018). Metcalfe’s Law as a Model for Bitcoin’s Value. Alternative Investment Analyst Review, 7(2), 9–18. The primary published treatment of network-value scaling in Bitcoin.
Wheatley, S., Sornette, D., Huber, T., Reppen, M., and Gantner, R. (2019). Are Bitcoin Bubbles Predictable? Combining a Generalised Metcalfe’s Law and the Log-Periodic Power Law Singularity Model. Royal Society Open Science, 6(6). Combines network-value scaling with bubble diagnostics, and is unusually explicit about the limits of both.
Griffin, J. and Shams, A. (2020). Is Bitcoin Really Untethered? Journal of Finance, 75(4), 1913–1964. A methodological model for how a specific, falsifiable claim about crypto market structure should be tested.
On the technical indicators examined
Wilder, J.W. (1978). New Concepts in Technical Trading Systems. Trend Research. The original specification of the relative strength index, used here as published rather than as commonly modified.
Edwards, C. (2019). Hash Ribbons and Bitcoin Bottoms. Capriole Investments. The origin of the hash-ribbon construction tested in the mining section of the suite.
Data as of September 2026 · Sources: the Crypto Exponentials daily snapshot (Blockchain.com, Coin Metrics, Coinbase, Deribit, OKX, CFTC, FRED, Alternative.me, issuer disclosures) · All figures independently recomputed in Python against the live snapshot prior to publication · Methodology, corrections and changelog: cryptoexponentials.com/tools/methods · akshinthalakk.com
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