The Multidisciplinarian

Introduction: A Historical Lens on String Theory

In 2006, I met John Heilbron, widely credited with turning the history of science from an emerging idea into a professional academic discipline. While James Conant and Thomas Kuhn laid the intellectual groundwork, it was Heilbron who helped build the institutions and frameworks that gave the field its shape. Through John I came to see that the history of science is not about names and dates – it’s about how scientific ideas develop, and why. It explores how science is both shaped by and shapes its cultural, social, and philosophical contexts. Science progresses not in isolation but as part of a larger human story.

The “discovery” of oxygen illustrates this beautifully. In the 18th century, Joseph Priestley, working within the phlogiston theory, isolated a gas he called “dephlogisticated air.” Antoine Lavoisier, using a different conceptual lens, reinterpreted it as a new element – oxygen – ushering in modern chemistry. This was not just a change in data, but in worldview.

When I met John, Lee Smolin’s The Trouble with Physics had just been published. Smolin, a physicist, critiques string theory not from outside science but from within its theoretical tensions. Smolin’s concerns echoed what I was learning from the history of science: that scientific revolutions often involve institutional inertia, conceptual blind spots, and sociopolitical entanglements.

My interest in string theory wasn’t about the physics. It became a test case for studying how scientific authority is built, challenged, and sustained. What follows is a distillation of 18 years of notes – string theory seen not from the lab bench, but from a historian’s desk.

A Brief History of String Theory

Despite its name, string theory is more accurately described as a theoretical framework – a collection of ideas that might one day lead to testable scientific theories. This alone is not a mark against it; many scientific developments begin as frameworks. Whether we call it a theory or a framework, it remains subject to a crucial question: does it offer useful models or testable predictions – or is it likely to in the foreseeable future?

String theory originated as an attempt to understand the strong nuclear force. In 1968, Gabriele Veneziano introduced a mathematical formula – the Veneziano amplitude – to describe the scattering of strongly interacting particles such as protons and neutrons. By 1970, Pierre Ramond incorporated supersymmetry into this approach, giving rise to superstrings that could account for both fermions and bosons. In 1974, Joël Scherk and John Schwarz discovered that the theory predicted a massless spin-2 particle with the properties of the hypothetical graviton. This led them to propose string theory not as a theory of the strong force, but as a potential theory of quantum gravity – a candidate “theory of everything.”

Around the same time, however, quantum chromodynamics (QCD) successfully explained the strong force via quarks and gluons, rendering the original goal of string theory obsolete. Interest in string theory waned, especially given its dependence on unobservable extra dimensions and lack of empirical confirmation.

That changed in 1984 when Michael Green and John Schwarz demonstrated that superstring theory could be anomaly-free in ten dimensions, reviving interest in its potential to unify all fundamental forces and particles. Researchers soon identified five mathematically consistent versions of superstring theory.

To reconcile ten-dimensional theory with the four-dimensional spacetime we observe, physicists proposed that the extra six dimensions are “compactified” into extremely small, curled-up spaces – typically represented as Calabi-Yau manifolds. This compactification allegedly explains why we don’t observe the extra dimensions.

In 1995, Edward Witten introduced M-theory, showing that the five superstring theories were different limits of a single 11-dimensional theory. By the early 2000s, researchers like Leonard Susskind and Shamit Kachru began exploring the so-called “string landscape” – a space of perhaps 10^{^}500 (1 followed by 500 zeros) possible vacuum states, each corresponding to a different compactification scheme. This introduced serious concerns about underdetermination – the idea that available empirical evidence cannot determine which among many competing theories is correct.

Compactification introduces its own set of philosophical problems. Critics Lee Smolin and Peter Woit argue that compactification is not a prediction but a speculative rationalization: a move designed to save a theory rather than derive consequences from it. The enormous number of possible compactifications (each yielding different physics) makes string theory’s predictive power virtually nonexistent. The related challenge of moduli stabilization – specifying the size and shape of the compact dimensions – remains unresolved.

Despite these issues, string theory has influenced fields beyond high-energy physics. It has informed work in cosmology (e.g., inflation and the cosmic microwave background), condensed matter physics, and mathematics (notably algebraic geometry and topology). How deep and productive these connections run is difficult to assess without domain-specific expertise that I don’t have. String theory has, in any case, produced impressive mathematics. But mathematical fertility is not the same as scientific validity.

The Landscape Problem

Perhaps the most formidable challenge string theory faces is the landscape problem: the theory allows for an enormous number of solutions – on the order of 10^{^}500. Each solution represents a possible universe, or “vacuum,” with its own physical constants and laws.

Why so many possibilities? The extra six dimensions required by string theory can be compactified in myriad ways. Each compactification, combined with possible energy configurations (called fluxes), gives rise to a distinct vacuum. This extreme flexibility means string theory can, in principle, accommodate nearly any observation. But this comes at the cost of predictive power.

Critics argue that if theorists can forever adjust the theory to match observations by choosing the right vacuum, the theory becomes unfalsifiable. On this view, string theory looks more like metaphysics than physics.

Some theorists respond by embracing the multiverse interpretation: all these vacua are real, and our universe is just one among many. The specific conditions we observe are then attributed to anthropic selection – we could only observe a universe that permits life like us. This view aligns with certain cosmological theories, such as eternal inflation, in which different regions of space settle into different vacua. But eternal inflation can exist independent of string theory, and none of this has been experimentally confirmed.

The Problem of Dominance

Since the 1980s, string theory has become a dominant force in theoretical physics. Major research groups at Harvard, Princeton, and Stanford focus heavily on it. Funding and institutional prestige have followed. Prominent figures like Brian Greene have elevated its public profile, helping transform it into both a scientific and cultural phenomenon.

This dominance raises concerns. Critics such as Smolin and Woit argue that string theory has crowded out alternative approaches like loop quantum gravity or causal dynamical triangulations. These alternatives receive less funding and institutional support, despite offering potentially fruitful lines of inquiry.

In The Trouble with Physics, Smolin describes a research culture in which dissent is subtly discouraged and young physicists feel pressure to align with the mainstream. He worries that this suppresses creativity and slows progress.

Estimates suggest that between 1,000 and 5,000 researchers work on string theory globally – a significant share of theoretical physics resources. Reliable numbers are hard to pin down.

Defenders of string theory argue that it has earned its prominence. They note that theoretical work is relatively inexpensive compared to experimental research, and that string theory remains the most developed candidate for unification. Still, the issue of how science sets its priorities – how it chooses what to fund, pursue, and elevate – remains contentious.

Wolfgang Lerche of CERN once called string theory “the Stanford propaganda machine working at its fullest.” As with climate science, 97% of string theorists agree that they don’t want to be defunded.

Thomas Kuhn’s Perspective

The logical positivists and Karl Popper would almost certainly dismiss string theory as unscientific due to its lack of empirical testability and falsifiability – core criteria in their respective philosophies of science. Thomas Kuhn would offer a more nuanced interpretation. He wouldn’t label string theory unscientific outright, but would express concern over its dominance and the marginalization of alternative approaches. In Kuhn’s framework, such conditions resemble the entrenchment of a paradigm during periods of normal science, potentially at the expense of innovation.

Some argue that string theory fits Kuhn’s model of a new paradigm, one that seeks to unify quantum mechanics and general relativity – two pillars of modern physics that remain fundamentally incompatible at high energies. Yet string theory has not brought about a Kuhnian revolution. It has not displaced existing paradigms, and its mathematical formalism is often incommensurable with traditional particle physics. From a Kuhnian perspective, the landscape problem may be seen as a growing accumulation of anomalies. But a paradigm shift requires a viable alternative – and none has yet emerged.

Lakatos and the Degenerating Research Program

Imre Lakatos offered a different lens, seeing science as a series of research programs characterized by a “hard core” of central assumptions and a “protective belt” of auxiliary hypotheses. A program is progressive if it predicts novel facts; it is degenerating if it resorts to ad hoc modifications to preserve the core.

For Lakatos, string theory’s hard core would be the idea that all particles are vibrating strings and that the theory unifies all fundamental forces. The protective belt would include compactification schemes, flux choices, and moduli stabilization – all adjusted to fit observations.

Critics like Sabine Hossenfelder argue that string theory is a degenerating research program: it absorbs anomalies without generating new, testable predictions. Others note that it is progressive in the Lakatosian sense because it has led to advances in mathematics and provided insights into quantum gravity. Historians of science are divided. Johansson and Matsubara (2011) argue that Lakatos would likely judge it degenerating; Cristin Chall (2019) offers a compelling counterpoint.

Perhaps string theory is progressive in mathematics but degenerating in physics.

The Feyerabend Bomb

Paul Feyerabend, who Lee Smolin knew from his time at Harvard, was the iconoclast of 20th-century philosophy of science. Feyerabend would likely have dismissed string theory as a dogmatic, aesthetic fantasy. He might write something like:

“String theory dazzles with equations and lulls physics into a trance. It’s a mathematical cathedral built in the sky, a triumph of elegance over experience. Science flourishes in rebellion. Fund the heretics.”

Even if this caricature overshoots, Feyerabend’s tools offer a powerful critique:

1. Untestability: String theory’s predictions remain out of reach. Its core claims – extra dimensions, compactification, vibrational modes – cannot be tested with current or even foreseeable technology. Feyerabend challenged the privileging of untested theories (e.g., Copernicanism in its early days) over empirically grounded alternatives.
   
   
2. Monopoly and suppression: String theory dominates intellectual and institutional space, crowding out alternatives. Eric Weinstein recently said, in Feyerabendian tones, “its dominance is unjustified and has resulted in a culture that has stifled critique, alternative views, and ultimately has damaged theoretical physics at a catastrophic level.”
   
   
3. Methodological rigidity: Progress in string theory is often judged by mathematical consistency rather than by empirical verification – an approach reminiscent of scholasticism. Feyerabend would point to Johannes Kepler’s early attempt to explain planetary orbits using a purely geometric model based on the five Platonic solids. Kepler devoted 17 years to this elegant framework before abandoning it when observational data proved it wrong.
   
   
4. Sociocultural dynamics: The dominance of string theory stems less from empirical success than from the influence and charisma of prominent advocates. Figures like Brian Greene, with their public appeal and institutional clout, help secure funding and shape the narrative – effectively sustaining the theory’s privileged position within the field.
   
   
5. Epistemological overreach: The quest for a “theory of everything” may be misguided. Feyerabend would favor many smaller, diverse theories over a single grand narrative.

Historical Comparisons

Proponents say other landmark theories emerging from math predated their experimental confirmation. They compare string theory to historical cases. Examples include:

1. Planet Neptune: Predicted by Urbain Le Verrier based on irregularities in Uranus’s orbit, observed in 1846.
2. General Relativity: Einstein predicted the bending of light by gravity in 1915, confirmed by Arthur Eddington’s 1919 solar eclipse measurements.
3. Higgs Boson: Predicted by the Standard Model in the 1960s, observed at the Large Hadron Collider in 2012.
4. Black Holes: Predicted by general relativity, first direct evidence from gravitational waves observed in 2015.
5. Cosmic Microwave Background: Predicted by the Big Bang theory (1922), discovered in 1965.
6. Gravitational Waves: Predicted by general relativity, detected in 2015 by the Laser Interferometer Gravitational-Wave Observatory (LIGO).

But these examples differ in kind. Their predictions were always testable in principle and ultimately tested. String theory, in contrast, operates at the Planck scale (~10^19 GeV), far beyond what current or foreseeable experiments can reach.

Special Concern Over Compactification

A concern I have not seen discussed elsewhere – even among critics like Smolin or Woit – is the epistemological status of compactification itself. Would the idea ever have arisen apart from the need to reconcile string theory’s ten dimensions with the four-dimensional spacetime we experience?

Compactification appears ad hoc, lacking grounding in physical intuition. It asserts that dimensions themselves can be small and curled – yet concepts like “small” and “curled” are defined within dimensions, not of them. Saying a dimension is small is like saying that time – not a moment in time, but time itself – can be “soon” or short in duration. It misapplies the very conceptual framework through which such properties are understood. At best, it’s a strained metaphor; at worst, it’s a category mistake and conceptual error.

This conceptual inversion reflects a logical gulf that proponents overlook or ignore. They say compactification is a mathematical consequence of the theory, not a contrivance. But without grounding in physical intuition – a deeper concern than empirical support – compactification remains a fix, not a forecast.

Conclusion

String theory may well contain a correct theory of fundamental physics. But without any plausible route to identifying it, string theory as practiced is bad science. It absorbs talent and resources, marginalizes dissent, and stifles alternative research programs. It is extraordinarily popular – and a miscarriage of science.